Encyclopaedic Companion to Medical Statistics Second Edition
Edited by BrlanS.Ev.nt Professor Emedtus, KIIig's CoIIege,...
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Encyclopaedic Companion to Medical Statistics Second Edition
Edited by BrlanS.Ev.nt Professor Emedtus, KIIig's CoIIege,. London, UK
and ChrIstopher R. Palmer
DItecIot Of the CenIte for App1Ied MetJIt:!II StatIstics, UnIvetsIty of CsmbIIdgs, UK
With a Foreword by Richard Horton
~WILEY AJohn Wiley and Sons, Ltd, Publicalian
This editiaa 6rst palllisbcd 2011 l' 2011 . . W'1Iey a. Saas. Ltd
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JaIaa Wiley a: Saas IJd., The Alrium,.Soulbma ~ CIUc:hestcr. West Suaex, P.OI9 ISQ. ",lted KiQIIIom Far demOs 01_ PaW editOrial a8Iccs, ·far CIIIIaaIa' ~I aacI far iDformIIdaD . . bow copyriPt IIIIIaW iD dIis book please see oar wbsik: at www.wiley.ODID.
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All riPIs raerwd. No part of Ibis publiadi_ may .., n:pmduI:cd. stmaI ia a Idrieval SJStaII, GI' tnInsIaittaI, in lIlY farm GI' by Ibc UK .CapyrqIII~ Dcsipi
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Wiley also publishes its boab fa a ~ of elOCInIaic fOlllllll. Same C'OIIIeDt dial appears in priDt may ~ .., ·a\llilable iD ckcIraaa"e books. DcIipaIians used by compIIIics 10 cIistinpi'lb 1hcir pnIducIs In oftca clabncclll tradcmub.. AlIIaad DIIIIICS IDCI pmdud _ Used in dIis book an: InIIIc: Dillie&, scrvD -ks, Indc:IiiIub ar.staaI bldelDlrb of Ibeir 1apCCtiw: __II.. The pJbIidM:r Is DOl IlSOCialed wida aa)' pmduca or veaclar IDeIItiaDad in dill book. 'dais public:adaa iI.Biped to pnwide accurIIe aad authmi~ . iDfonnaIiDn ill IqIId to subject maIIa ~ Il is sold _ die .......ini thai the- publisher il DDt cappel iD tadi.iq ...,reaiaaallClvic:cs. If JIR)fasiaaaI acIvice or ada aped usisIaace is .aiui1ed..1hc ~ of a ~ profcaional ~ be BDqbt.. .
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Librory"fl/CIIIIBWU OIlIllo'''''''·l'IIbIicaliDn Dtlltl The CDC)'CIopaadic campaaiaD to ..... staIiiIiI:s I cdiIaI by Brim S. Emtt aad CJn1apIaer R. PahDc:r; with • fcRwanl by RicbanlIIadaIL - 2IId ell.
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lacludes IIiIIIiDpapIIic n:f'cmxcl. ~ ..... Elicyclopaalic Campaaian .10 MtcUc:.I Stlllisties, ....i · rcadibIe ~ or almost 400 sbdistical topicl ceatial to cam:III medical n:sean:b. Each catry _1Icca wriIIat by aa iDdiYidilal chasca far bath 1hcir expc:rIiIcia 1hc field aad tbdr abilitY to.CDIIUIIIIIIicale sbdilitical aIIICCpIS succ:cssrully 10 madical mtai"'lI.. Real a .....cs tiUm 1hc bIomcdicaI ~ ......... ililstndioas feam mID1ft)' entries, aad ~ cnu n:fmnciDI sipposts Ihc iader to ....,. CIIlrics"'-PRJvidai by puIiIisbu. . . ISBN 978-0470-61410-1 (!lib)
I. Medical ~Iopedjal I. Ewritt,. __. D. Palmer. aIrisIopbi:r .Rat,h. . (DNlM: l. S1aIiItics as ~"'s-EagIisIL 2. ~ 'J'bcaIaic~~ WA 13 E562 2010) RA409.ES2120IO 6Io.120~·
2010018141 A c....... 1tICCIId for this .... 1s IlftiIIbIc tiaai Ibc British LiInIy. PrinlISBN: 978-0470-61419-1 cPDF ISBN: 9'fI.O..470-ddD74-7
To Mary-Elizabeth Brian S. Everitt To Cailry-Joan, Lalll'a, Carolyn and David Christopher R. Palmer
Contents Foreword ........ Preface 10 the Second Edition I
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Preface • . . • • • . • . . • . • . . . . • • . . . . . • • . . . . . • . . . . . . • . . . . . . • . . . . . . • . . . . . . • . . . . . . • . . . . . • xiii Biographical Infonnalion on the Edilors ••••.••••••.•.••••.•.•••••••••••.••••••.•••••••••• xv
LiSl or Conbibtltors . • .. .. . . • . • • .. . .. • . • • .. . .. • • • .. .. . .. • . • .. .. . .. • . • .. .. . • • • • .. .. . .. • • • .. .. . .. • • • .. .. . .. • • I vii Abbreviations arad Acronyms ......... Xli Eocyclopaedle ColDpaaioD to Medical Statlsllcs A-Z . . • • • • • . . • • • • . . • • • • • • . • • • • • • . • • • . . . 1-491 I
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Foreword This cac:yclopaediac:ontains nocnlly ror 'Pe«~iew' .In my small comer of the medical statistical uni\lCnlC, Ibis seems Iikcagrasssinoromission.lnstead.lhcpn:x:cssorcw)ualing MSCIII'Cb papers is discussed under 'Critical appraisal'. Arc these two proc:edun:s synonymous? And. im:speclive or whether they 1ft or 8M not. should anybody cam? I believe Ibat peer review and critical appraisal do dilTer. that these dille.n:na:s mattcr a deal when considering the ways in which n:aclcrs should intClpn:l the medical Iitcral~ and lhat an undcnIandin, or these difrc~nces hclps to place medicaJ Slatistics in its proper (lCJftlext when surveying Ihc wide horizon of c:IinicaJ and public health n:scardI. Thc editors of this quite wonderfully rewarding uatise on slatisticaltenns havedcftncdcritical appraisal as 'the process of evaluatinJ; n:search n:poItS and assessing their contribution to scientific: knowledJ;c·. 'Ibis statement follows naturally from Ihc mean in, of the words 'criticism' (the an of judgiq)and 'appraisal' (lheestimationofquality). Tbatisto say. critical appraisal is an cstimation of wonh followed by some kind of judJ;ment- ajudt;ment that leans IIKR towards an art lhan a science. As a non-statistician, I rather wann to the precise imprecision of Ibis definition. Now consider the more commonly embeddc:d term 'peer n:vicw' and look how infcrior it is! Who is this anonymous idealised peer? Ocncrally. one would consider a peer 10 be an equal. somebody whocamc:s frum a groupcamparable to Ihat from which Ihc penon under scrutiny has cmcrgc:d. 1bis intellectual cgalitarian is subsequently setlhclask ofviewing apin (to take '~vicw' at its mosl literal meaning) the work underconsiclcration. But 10 view with what purpose? None is specified. Despite these practical shortcomings. editors of biomcclical joumals ~maiD wedded 10 "peer review'. Wc feci uncomfonablc with the notion of critical appraisaJ. The cmbodiment of peer ~view as a distinct scientific discipline is the series of inlcnlalional cOnJ;~sses devoted to peer n:vicw in biomedical pubUealion. or,aniscdjointly by JAMA and thc BMJ. These conpcsscs have spawned hundrals of abstracts. dozens orrescarch papers. and fourthemc issues or JAMA. They are enti~lycommendable in every WDy. For the cdilon of JAMA and the 8MJ, peer revicw encompasses a broad nmsc of activities: mechanisms of editorial decision making. toscthcr with their quality. validilY, and pncticality. online peer review and publication. pm-publication posting
,real
of infonnation. quality assuranc:c of ~vicwcrs and editors. aulhorshipand conlributanhip. conflicts or interest. scientific misconduct. peer ~vicw of grant proposals. economic aspects of peer ~icw. and the fUlU~ of scicntific publication. In other words. peer ~view is a ~mendously elastic concept. allowing editon to stretch it to mean whatever inle~ts them at a given (whimsicaJ) moment in lime and place. Indeed. its claslicity is seen by many of us as its ,~t ~th. ThcCODClCpI pows in richncss and undenlanding as our OWD appreciation of its complexity and nuance soars. 11le impenClrable nature of pccrnmcw. and the obscu~ and hardto-learn cxpertise iI demands. rceds our brilllc c,os. The notion of critical appraisal. by contrast. is far dUnner in meanin,. wilh much less room for cdilorial manipulation and BlP'Bndiscment. EVcn if peer review and crilical appraisal do diller. should anyone actually can:? Yes. they should. and for a very simple rason: the idea of peer ~icw is now bankrupt. Its ~tention as an operation within the biomedical sciences ~Rects Ihe inte~sts or those who wish to preserve their own pow« and position. Peer ~icw is fundamentally anti-democratic. II elcwtes the mediocre. It asphyxiates originality and it kills careers. How so? Peer ~view is DOl about intelli,cnt cnJ;agcment with a piece of rac~h. It is about defining the margins of what is acceptable and unaa::eptable to the ~vicwcr. 'I1Ie mythical 'peer' is bein, asked to view again. after Ihe cditor. the work in queslion and to oller a eomment about thc gcogaphical location of Ihat work on the map or existing knowledp:. If ~ is space on Ihis map, and providc:d the work does not disrupt (too much) the terrain cslablishcd by others. its location can be secured and marked by sanctioniq publication.lfthe disruption is toog~at. the wed's wish to seck a place of ~st must be "CIocd. Peer review is about the DleDeY of power to praervc csbIblished onhodoxy. It has nolhin, 10 do with science.•1 has cverylhinJ; to do with ideology - and the maintenance of a quiel Iifc of privilcp: and mysliquc. Instead. critical appraisal is aboul incrementally wedin, one's way towards lrulh'. It can new:r be about lruth itselr. The essencc of biomedical ~sean:h is cstimation. Our world ~sists CCltainly. Crilical appraisal is aboutlJ'aDsparcnt. measurablc analysis Ihat cuts a path towards grater precision. I. Honan.. R. 2002: Poi1pubItcaliCIII criticism _ dintcal ~. JAMA 217.2143-7.
the shapi", of
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RDREWORD _______________________________________________________________________
Critical appraisal refuSC5 to \'eil itself in the gaudy adornments that editors pin to peer re'liew in order to embellish their own imporlance in the carlography of scientific inquiry. A far more robust instrument critical appraisal is for that refusal. What do these differelK"CS tell us about the propcr place of medical statistics in biomedicine: today'! In my \'iew, as a lapsed doctor and a now wrinkled editor. medical statistics is the most important aspect of our critical appraisal of any piece of new resc.an:h. The e\'aluations by .so-called peers in the clinical specialties that concern a particular l'CSCW'Ch paper prm'ide valuable: insight into how that work will be reeeh'cd by a community of practitioners or scholars. Howevc:r. as an editor I am less intere:slc:d in n:ccpCion than I am in meaning:. I want a tough intcno~ation of new work before its publication. according to commonly a~reed standards of questioning - standards that I can sec and e',-aluate for myself. To return to my personal definition of critical appraisal. I want an estimation of quality combined with ajudgment.1 do not want a view from the dub culture of one particular academic discipline. The rc:jection of peer re\'iew by the
2. Horton. R. 2000: Common sense and fig~: the mc:toric of \'ulldity in medicine. Solisl Med 19, 3149-64.
editors of this elK')'dopaedia is therefore a triumph of liberty against the forces of confonnity. Yet still today. too much of medicine takc:s medical statistics for granted. Time and a~ain. we sec research that has dearly not bc:cn within a hundred miles of a statistical brain. Physicians usually make poor scientists. and physicians and scientists to~ether too onen play the: pari of amatc:ur statistician - with appalling consequences. The future of a successful biomedical research enterprise: depends on the f1ourishin~ oflhe discipline we call me:dical statistics. It is not at all clear to me that those who so depend on medical statistics appreciate either that dependence: or the: fragility of its foundation. If this magnificent elK'yclopac:dia can be deployed in the ongoing ar~ument about the: future of twenty-first century academic medicine. then not only the research enterprise: but also the public's health and well-being will be far stronger tomorrow than it is today. Richard Horton Editor. Lanc'el
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Preface Sialistical science plays .. ilDporlanl role in medical JaelRh. Indeed a major pall of lhc key 10 lhc pmgras in medicine tian lhc 17th ceatlll)' 10 the pn:scnl day has been the collcetion and valid inlCqRtalion of evidence.. panic... larly quantitative cvidence. pmvidccl by Ihe appIicalion of stalislical methock to medical inYeSlipiioas. Cum:nl medical journals ~ full of statislical lDIIICriai. both rdalively simple (for eumple.. t-lcsls. p-wlues.lincar lqIaSion) and. increasingly, mo~ complCJC. (for cxample. genenalised c:stimaliDl equalians. cluSla" analy. Ba)eSiaD IDClhods). The laller material reRects the vilnnl 5IaIc or stalistical research with many new mdhods having praclical implicati_s f~ medicine heiDI cIc~oped iD thc IasllWO cIcc&des ar so. Bul why is slatistics impallaDl in medicine? Some possible answers are: Medical praclice and medical rescan:h gcneralC IaJp amounts of clara. Such data an: generally full of uncertainly and \·arialion. and e&tIacling the "sipal· from lhc "Daisc' is usually nollrivial. (2) Medicine involves asking quclli_s lhaI have slraDg slalislical overtones. How common is lhc discasc? Who is especially likely 10 conInIcl a particular condition? Whal an: lhc chances thai a patienl diasnoscd with breast cancer will survive man: tha fi\IC yean? (3) The evaluation of campcliq In:allDCnts or pn:vc:alative IDCIISIRS relics heavily on slatillical cOllCc:pl' in both lhc clcsip and analysis phase.
(I)
Recognilion orlhc: importance ofstalislics in medicine has increased considerably in n:ecnl years. The lasl decade. in padicular. has seen the emergcnce of cvidence-based mccIicinc.., ..d with it the need for clinicians to keep one step ahead or lheir paticnts. lDay or whom nowadays ha\IC access 10 virtually unlimiled inronnation (lDuch ofil being virtual, yct SOnIC of it being limiled in its reliabilily). Comparcel with ~vious gencrations of medical students,. today's prc-cliniclil undergraduales arc heiDI taughl more about statistical principlcs than lhcir predecessors. Furthermore. today's clinical researchers 1ft faced (happily. in our vicw) with growing numbcn or biomedical journals utiBsing slatislical rcfCl'CCS as part of their peer Mview proccsses (sec amCAL APPRAISAL and STATImCAL REFEllEEDKJ). This enhances the qualily oflhe papersjoumal editors select. although from the clinical n:scardJcr's
pcnpc:clive it has lDade publicalion in leading journals more challcnginglhan ever befOM. So slalistics is (and an:))RYalcnl in the medical world now and is sello ranain so ror the future. Clearly. clinicians and medical n:scan:hcn need to know somcthiq about Ihe subject. cven ifonJy 10 maIcc their discussion with a friendly Slalislician more rruitful. The article on consulting a stalilr tician quolcs one of the fGRfatbcn or mocIenI slalillics, R.A. FISher who- back in 1938. obsc:ncd wryly: "To conn,lt lhe $Itll&lIcilBr tlJln till e."cpnimerrl isjin&lred u often merely 10 ale him ID conduct II po.,-mor'em e.'ttlmintlliDR. He Cllll per/uJps my ...·btlI tire e.'fpe,imerrl dim of.' Thus. one or our hopes for the usefulness and helpfulness of the EncycloPllffdic COmptllliDIf 10 MediCtlI Sltlli,sl;cs is lhat it may SCrYC 10
cncaurqe both productive and timely intaaclioas bcawcca medical racan:hc:rs and statiSlicians. Anolhcrsincc~ hope is that il ftlls a pp between, on the one hand. lextbooks thai delve into possibly 100 much theory and. on the olhcr haad.. shader cliclianarics thai may not necessarily focus on Ihc needs of medical racan:hc:n.. or else have c:alrics Ihat an: IanlalisiDlly succinct. 1b meet these ends. lhc presenl ~f cn:nce wark conlains concise. informative.. n:lali~ly nontechnical. and hence, we IrUsl. readable acc:ounlS of over ]So topics ccatrallo modem medical statistics. Topics are coVCRd either brieRy or mo~ extensively. iD general. in accordance with the subject matter's pcn:eivcd ilDportance. although we acknowlcdlc then: will be disagn:cmcnt. incvilabJy. about our ChaiClC of DIIicle lengths. Many entries benefit from containing real-life, clinical exalDples. Each has been wriltcn by an individual chosen not only for subjecl-maller expertise in the ficld bUI.just as ilDportantly. also by ability 10 communicale statistical concepls to olhcn. 11ac extensive cl'OSlrrefcn:nc:ing supplied usiq SMAU. CAPII'ALS 10 indiclllC tcnns thai appear as separate entries should help the radcr to find his or her way amuncI and also serves to point out associated topics thai might be of intcral elsewhere within lhc EncycloptJedic Comptllf;tIII. All but the shadcst caines contain rerCI'CIICCS to fUJthcr resources when: the interested n:aclcr can learn in paler cIcpIh about Ihc palticular topic. Thus. while hoping this work is found to be mostly comprehcasiblc we do nol claim illo be rullyCGIDprchcnsi~. As c:o-editan we lake joint n:spansibilily far ..y enurs ('sins or commission') and would positively weIc:omc sugcslions
xiii
PREFACE _____________________________________________________________________ ror possible new topics to consider for futw-c: inclusion to R:ctiry perceivc:d missing entries ("sins or omission'). Our thanks ~duc to numerous people - first. to all onhe many conlributors for providing such excellenl material. mostly on time (mosaly!) with panicular gratitude: extended to those who contributed multiple &nicles or who handled requests for additional &nides so gracefully. NeXI. we upprcciatc:d Ihc lrcmendous and indispensable effom of staff at Arnold. cspccially Liz Ooostc:r and Liz Wilson, and not least ror their remaining calm during an editor's moments or anxiety and neurosis about the enlire projecL In addition we would like to thank Harriet Meteyard for her eonslanl support
and encouragemenl throughout the preparation of this book. F"mally. our family memben deserve especial thanks ror ha\ing been exba toleranl of our lime spenl on developing and executing this extensive projecl from beginning 10 encLll is our hope thai Ihe Encyclopaedic- Companion pnn'cs all these efforts and sucriHces to be well worthwhile. becoming a userul. rqularly-thumbc:d reference added to the bookshelf or many or those involvc:d in contemplating. conducting or contributing 10 mc:dical rcscan:h.
Brlaa S. Everitt aDd Clartstopber R. P......r /tlnlllllY 2005
Biographical Information on the Editors BrI_ S. Everitt - Professor Bmerllal, KIDR·s eo... Londo.. After 3S years al the: InSlitulC of Psychiatry. University ofLondoD. Brian Ewritt n:tired in May 2004. Author of approximately 100 journal articles and O\'Cl'SO books on statistics. and also co-c:ditor of SllIlisllml Melhods in Met/· im/ Reselll'cir. Writing continues apace in n:lin:ment but now puncluatc:cl by lenn~ walks ia the counlry.luitar playing and visits to the Dna. rather lban by committees, committees and mon: committees.
Cbrlstapher R. Palmer, roundins Din:ctor of Cambridge University's Centn: for Applied Medical Statistics. rqularly teaches and collabanlc:s with cum:al and fuaun: cIoctan. His first clcln:e was from Oxford. while graduate and postdoctoral studies \VCR in the USA (at UNC-Cbapel Hill and Harvani). He has shined frvm mathcmaticaltowards applied Slatistics.. with particular inten:st in lheethics ofclinical trials and Ihe use or ftexible designs whenever appropriale. Fundamentally. he likes to promote soUDd statistical thinking in all areas of medical raean:h and hopes this volume might help towards dlat end. Chris SClrved as Deputy or Acting Editor far Slatistics In Medicine, 1996-2000. and is a longstandinlslatistical n:viewer for 71re Lancel. He and his wife have three childn:n they ClClllsider to be IIICR than statistically sipificant.
xv
List 01 Contributors K. R. Ab...... (DA). Cenln: for Biaslalislics aad Ocnelic. BpiclemioJOI)', J)cpaIbDent.ofHeallh Scic:nccs. UniwDit)' of Leicesla', LBI 7RH. UK
....,icestc:r.
Calla ....... (CB), Cli.aI nial Servic:e JJnil and
I.ac)r M. CarpeD.... (LMel, DeparlmeDt of Public Heallh.
Univenil)' of oxronl,. and Nullield CoIIcp,. oxranl ox I INR UK .
iuaa CIdaD (SC), Respiratory Epidc:miok., aad Public Health. Imperial College. Emmaaucl
Ka~. Building.
EpiclcmioJogicai Studies Unit (CTSU). Richanl Doll Buildilll. Olel Raad Campas. Raosevelt Drive. oxranl OX] 7LP,. UK
Manraa Road. LaacIon SW3 6LR,. UK
Alua ....... (AB), QuantilatiWl Scienc:cs. OIuoSmith-
LandaD WC1N lEH,. UK
Kline. Medicines Rcscarch Ce~ Gumaels Woad Raacl. Stevcaace. Hertrordshill' SOl lNY. UK
'11m CelIe (TJC), MRC C'enIrc of EpidemioiOD rar aaJcI Health. UCL Instiblte or Child Health. 30 Ouilrord SIn:et.,. Chris CGftOI8D (CCo), J)cpaIbDent of Madlematies and Los-. UT 84322-3900.
Statistics. Ulall Slate Univenity,
TlJI De Ble (TOB), ISIS Rc:sean:. 0nIup. Buildiq 1. UniWlnity of Sauduunplon. SouIb....pIaI S017 IBJ. UK KII.... Bjork CD). Primelric:s. Inc:. AmIcIa, Colanclo, USA (btheOprimebics.net)
J. MuIID ....... (JMB), Pmfessor or Health SlDIistics. DepadJnent of Health Sciences. UniWlmity of yadt,
HesliDgtaa. yadt YOlO SDD,. UK Ma.......... (MtB), DivisiOll of Bioltatics. AnIoId School of Public Heal.... Univenity of South Carolina. 800 Sumter Sbeet. Columbia. SC 29208. USA. and also Unit of BiosIaIisIics. InstitulC of BnvinHlll1ClllaI
Medicine. Kmulinslca Institutet Nobels ric 13. Stackholm. Sweden MkIIIUe Bndley (MMB), Health Ial'onnatiaa and Quality AUlharit)', Oc:orp's Court. Ocoqe's lane. Dublin 7.1n:1anc1 ........... (SB), Departmenl
or Sacial Medicine.
UniWlnity or Bristol. C_ynge HaD. Whiteladies Road. Clifton, Brislol Bsa 2PR. UK Marc aa,.. (Ma), Intenational Dna, DeWllapmenl "stitute (IDDI). 30 avenUc provineialc..
1340 Louvaia-la-Neuve. BelPum
M..J. CampIIeII (MJc)' School of Heahh aiad Related ReseaKh. University of Sheflielcl. Resent Court. 30 Relent Sbeet. SlIellleld SI 4DA,. UK
USA
or
NeIIo CrIIIIaaIaI (NC), UC Davis Departmc:Dt Slalisties.. 360 ICar Hall. One Shields A~ Davis.. CA 9S616. USA
Sanb CnaIer (SRC), MRC urec:ounc EpidelllioiOlY Unit. University or Southampton,. Southampton
General Hospital. Southampton $016 6YD, UK CaraIe O.mml" (CLC). 'I'be University of BinniaPam. Departmeat ofPublic Heal.... BpidemiolOl)' ancIBiotali*s, go VlIIL'ICnt Drive. Ecl&ballOll. Binni~ B 15 lTH Geo.... DllYII,-8mUb (ODS), Schaol or Social and Communit)' Medicine.. Uniwnit)' of' Bristol,. Oakfield Hause. Oakfield Onnre. Bristol BSS 2BN, UK Sbaaa Da, (SO), Raclae Products LilnilCd.. Welwyn 0anIen
Cit)'. HertfonIshiM. AL7 ITW. UK.
DaaIeIa·De A"'IIII (DBA), Statillics.. Modellin& and Economics Departmc:llt. Healdl Pmta:tion Apncy, Cenln: far Infections. Landon and MRC BiCl5lalistics Unit. Jnstilute of Public: Health. Uniwnity Pantie SilC. Robinson Way. Cambridp: ca2 OSR, UK
J......... Dee.. (JD), Public Health. EpiclcmioJogy and BiastatiSlics. Univenit)' or Binningham. EcIgbasIon. Birmingham BI5 21T. UK 0 ....... Daaa (OD), Health Scienc:cs Resc:an:b Gnlup.
, ..... R. C......ater (JRC). Mcdic:aI SlaIistic:s Unit.
London School or Hygiene and 'l"rapkal Medicine:. Keppel Sbeet,. Lonclan welE 71fT. UK
Schaal or Canmaunily Based Medidae, UniWlnily of Manchester,. lean McFarlane Buildin& Oxford Road,. MaacbesIer MI3 9PL. UK
xvii
USfOFCONTRlmnoRS _________________________________________________________
Daua E8Itoa (DE), Department of Publi~ Health and
THY Johnso. (TJ), MRC Biostatistics Unia.lnslitute
Primary OR, University of Cambridge. SlI1Ingeways Resean:h I..abanlory. Worts Causeway. Cambridp
CBIIRN. UK
of Public Health. University Fonie Site. Robinson Way, Cambridge CB2 OsR. UK a MRC Clinical Trials Unit. 222 Euston Road. London. NW 1 2DA
Jo....... Bmbenoa (JE), Cinical Trial Servitle Unit and Epidemiological Studies Unit (CJSU). Ricbard Doll Building, Old Road Campus. Roosevelt Drive. Oxfard OXl
Karea KaIMIar (KKa), Department of Mathemalics. University of Colorado at Denver. PO Box 173364. Campus Box 170. Denver. CO 80217-3364, USA
7~UK
IUcharcI EauIey (HE), Health Sciences Resean:h Oraup.
School of Community Based Medicine.. University of MancheslCr. JeaD McFarlane Building. Oxford Raad. Manchester M 13 9Pt.. UK Bri. . S. Everlll (851£), Biastalistics Dcpadment. Institute of Psycbially. Denmadt Hill. London SES lAP. UK David FaraaII (OF), Depadment of Statistics. Univenity of Haif... Haifa 31905. Jsrael
lC.,.........•• lC.bn (KlC.), Department of Biostatistics and Medical Informatics, University of WISConsin Medical School. 60D Highhiad Ave., Madison. WI 53792-4675, USA bib Kina (RlC.)t School of Mlllhematics and Statistics. Mathematit:al Institute. UnivcrsityofSt Andrews. Fife KYI6 9SS. UK " WoJlek IC.JozaDDwsti (WK), School of Engineering, Mathematics and Physical Science. University of Exeter. Harrison Building. North Park Road. Exeter EX4 4QF. UK
Health and Health Policy. Division of CommuniI)' Based Sciences. University of GIIISIOW. GlasJow G128RZ, UK
RaDjlt LaD (RL), Warwick Emergency Care and RebabililaliCID. Division of Health in the Community. Warwick Medical School. Univenity of Warwick.. The PannhoWie. Gibbet Hill Campus, Coventry CV4 7AL. UK
81. Gaet.......ur (EO), Department of Applied Mathematics and Statistics. OIIent Universaly. Krijgslaan 281-89,9000 Ohcna. Belgium
Sabine Landau (SL), BioslDlislics Department. Institute of Psychiatry.. King's College. Denmark Hill. London SBS lAP. UK
AlKlnw Orl..e (AO), Division of Health a Social Can: Research. Depanment of Primary ~ and Public Health Scieaces. School of Mc:dicine.. King's College. Floor 7. Capital House. 42 Weston Loadon SEI 3QD. UK
Andrew 8. La. . . (AL), Division of Bioslalistics and Epidemiology, College of Mectacine. Medical University of South Carolina, Charleston. SC 29415. USA
W. Harper GUDIOur (WHG), Section far Public
sa.
Julilua P. T. ......_ (JPTH), MRC Biostatistics Unit. Institute of PUblic Health, University Forvie Sileo Robinson Way. Cambridge CB2 OSR. UK 11Ieodore .. HoIfanl (TRH), Division ofBiosiatistics. Yale School of Public Health~ Yale.. New Haven. CT 06520. USA HaUls (SH), AstraZc:aeca, Parklands. Aldedey Part. Macclesftclcl. ~eshire SKIO 4TF. UK
SaB)'
Tonte. Hotbana (TH). Institut fUr Slalistik. LudwigMuimilians-Univenitit MUnchen. LudwiplraS&e 33. DE-80S39 Miinchen. G:nnany Hazel 1_ldp (HI), MRC Lifecounc Epidemiology Unit. Uni~ty of Southampton, SouthamplOD Cieneral Hospital. ~~nSOI66YD.UK
Marwn Leese (ML), Health sCrvitle and Population Resean:h Department. Institute of Psychiaby, King's College. Denmark Hill. Loncloa SBS lAP. UK
AmI1 Lyada(AGL), DeparlmentofOncology. University of Cambridge. Li Ka Shing Cenam., Robinson Way. Cambridge.. CB20RE. UK Cyrns M..... (CM), President. Cytcl Software Corporation. 675 Massachusetts Avenue. Cambridge. MA 02139, USA RI..... Morris (RM), Department of Primary Can: and Population Health. UCL Medical SdJooI, Royal Free Campus, London NW3 2PF. UK Paul M......... (PM), Department" of Statistics, The University of Auckland. Private B8I92019. Auckland. NewZcaland
_______________________________________________________
CIIrIstopIIer R. ......r (CRP), J)epadlDent of Public Health and Primuy Care, Institute: of Public Health. Uni~nity Fantie Site. Rabiason Way. C8mbridp CB2OSR.
USTOF~~
Aaden SknIadIII (AS), DiYisiem of EpidcmioloJy. Norwepua InsIituteorPublic Health. PO Box 4404 Nydalen. N~. Oslo. Nanvay
UK
NIaeI Smeetaa (NCB). Kina's CoIlqe London. Max ......... (MP), MaC CUnicai Trials Unit. 222 Busloft Road. London NW 1 mA. UK
Departmc:Dt of Prillllll)' Care and Public Health Scieaces.. DiYisiem of Heal... and Social Cam Rc&eaIdI. 7th Floor Capital Haase. 42 Weston SlRIe~ Landon
Nlla ..... tNP), Cytel Softwan: Carpanlioa. 615 Massachusetts A\lellue. C'ambridp. MA 02139-3309, USA
3QD.UK
sal
NIaeIStdanl (NS), Wanvick Medical Schaol, UniYersilyof
J_a Pow-UP), Dcpanmc:at of Public Heallb and Primary
Warwick. COW:nII')' CV4 7AL. UK
Iaslitalc of PubUc Health.. Uni~ly Fcnie Site. Robinson Way. C8IIIbriqc Ca2 OSR. UK
Joaat. . . . . . . (JS), School of Social and
ellie,
P. PracaIt (pP), Faculty of Malhematical Studies, UniWl5ity or SauahamplOD. SouIhaaaplOft SOl7 IBI. UK SopIda ............. (SRH). Graduate School of Educatioa and Gndu_ 0nJup in Bi~. UniWl5ity or California. Berb1ey. 3659 Tolman H•• Califomia 94720. USA and InstilUte of Educalion. UniWl5ily or London
8m ...... (BR), Department
or SIalistics.. Uni~ or
Medicine. Uni~nily or BristoL Canynge HaIL 39 Whatley Road. Bristol BSS lPS, UK
Comaumil)'
.......... SWaIIDa (88), Swedish Business Schaoll Slalislics. oR::bro Univenily. 0n:In. Swedc:n
M ...... SJdes(MS), MRCClinicai Trials Unit. 222 EUSloII
Road. I..aDcIoa NWI 2DA. UK J......, Taylor (NOT), Depanmc:at or BiaslalilliCs. Univenity of Michipn. 1420 WIIIhiDIton Heilhts. Ann Arbor. MI4BI09-2D29, USA
Haif.. Haifa 31905. Israel
ShaaII . . . . . (sas), MRC BiasIalislic:s Unit. Institute of Pablic Health, UnivCnily Fonic Site. Robinaaa Way.
Kale TIIIIaa (KT), School or Social and Comm_ily Medicine. Uni~ty of Bristol, OmYlile Han, 39 Whalley ~ Bristol BSS 2PS. UK
Cambridge CB2" OSR, UK M ........ (MRS), Division of aiaslalistics.. Uniwnity of Califamia, 185 8c:n)' SIreel. Suite 5100. San FraDcisco. CA 94107, USA
PraI..,. .........art (PIe), CyteI Software Carpanlion. 675 MassachuseUs Avcnue.. Cambriclce. MA 02139-3309. USA ............. (SS),DepartmentofStlllistics. The Uni~ity of Olascow. Olasgow 012 8QQ. UK ~
SIuIID (PS), Deputmcllt of Psychialr)'. 11Ie Uni~ily of Hoa& Kan" Queen Mill)' Haspital, 102 Pakfulam ReI.
HOIIIICaIl&
c .... Sbarp (CS), Computiq Deputment. Institute of Psychially. Daunut Hil~ LoncIaa se 8AP. UK Anid SjalaDder (AlS,. Depadment of Medical Epiclemiolo" and Biasllllillics.. Karvlinsb InstilUlet. Nabels Vic 12A. 171 17 Stockholm. Sweden
81t1ua TGID (BT), MRC Biaslalistics Unil.lnstilUle of Public Health. University Fanie Site, Robinson Way. CambridJe
CB2OSR, UK
.
ReIM!ca 1'araer (RT), MRC Biostatistics Unit. Institute
or Public
Health, Uniwnily Fame Site. Robinson Way. Cambrid&e CB2 OSR, UK Aady V. (AV), Bio.dptista 0nJup. Uniwmdly or Maachcster, Oxfanl Road. Mancheller M13 9PL. UK
SII,Ia V...........t(SV),Gheal Uni~lSity, DcpLof AppIic:cI Mathematics and Computer Science. Krijplaan 281, S9, 8-9000 Ghent, BelPum Sanb L Vowier (SL\I), BioinfCll1lllltics CoR, Cancer Racan:h UK. Cambridge Rescan:h lnIIitute, Robinson Way. Cambridp CB2 ORE., UK
Stepbla J. W...... (SJw)' Medical SIaIistics Graup. School or Health and Related Raarch, University of Sheffteld. Regent Court. 30 Repnl Stn:et. Shemeld
SI4DA.UK
xix
USTOFCONTRIBUTORS _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ __
J.G. Wheeler (JG\V), Quanticate Ud. Bevan House. 9-11 lUi. UK Bancroft Court. Hitchin. Herts.
J .... \VII. . (JW), 1710 Rhode Island Ave. NW. Suite 200.
Bnmdon WbItcbI!r (aW). Clinicallmaginl Centre.
Mark Woad....... (MW" The George iMlibiac for
GluoSmilhKliae, Hammersmith Hospital. Du Cane Road. Lonclaa WI2 OHS. UK
Inlemalional Health. PO Box M20I. Misscaclen Sydney NSW 2OSO, Australia
sas
laD WhIte (IW), MRC Biostatistics Unil.lnslitulc or Public Univenit)' Forvie SiRe. RObinson Way. Cambridge
Health.
CB2OSR. UK
Washington DC 20036. USA
Road.
Ra-F_ Yeb (BY), University or California San Fl'IIIICisco. Campus Box Number 0560. Soo PanlB!isus" 420 MU-W. San Francisco, CA 94143-0560. USA
Abbreviations and Acro.nyms ACES ACET
AD AI AlC ANCOVA ANOVA AR
ARMA AUC
BlC BUGS CACe.
CARr .CAT CBA
CEA CI CONSORT COREe CPMP
CPO Cd CRM CSM .CUE CV
CWT DAG
DALY DAR DeAR DDD DE OaF
DIC DM DMC DIMC I)WT
Actiw conbvI cquivalcnc:c &Iud, Ac:Iiw COIIIIVi cqui~ I&:It Adapliw des.ip Altildal inlellipnc:e Alaike's information Crilaion AnaI,sil or COWIiaDt!e Analysil or variance AuloJqn:sSive Aulolqlaslve lIIDVinI'avcrap Ala " ' r c:urYe Ba)'Clian infonnaliaft crilCrian BaycSiaD inraa.ce Usia& Gibbs SIImpIinc (softw8re) CompUer awnp causal ell'ect Classiftcal~n and RpasiDn ftc
DZ 88M BOA EM
Diz)'lGlic EvicIencc-bued aalicinc BxplanlOl)' data analysis
£MEA
Ell...... Medicines EwllIIIIioa Apacy Food and DIu& Adminillnlliaft OcneraIised additive madel GencnlilCd csliaIaliDl eqlllltioDs CJeaeraI t'CItility nile
CoaapuICr..-laplive tcsIiJII Cosl-bc:neftl ",,.1 Cosl-ctrec:li--. analysis Caiaftdencc inIavaI
ORR GWAS
CGasolidalioa of s&ancIanIs or ftpIItinJ IriaIs ~:OI1ice
roi.RaeaIdI
FDA GAM
Gi!B GFR GIS GUM
GLMM
HALE
HMM
HPDl HREC HRQo~
IBD.
CaaunillCC fal' PmpricIary Medicinal Praducll Coiaditiaaal )RdicIiYC- onIi...e
ICC
"p
Dalaminill& Dada.monitorial cammilfeo
Data and saf'c:Iy monilariD& cammiuce DiI!Clde wavclcllnlnlf'orm
~ infOl1ll&llion sysICID
Gcnaalisallinear. illlenK:tiw .modcJIilll (SDftWIR)
GUMM GLM
Ethics ComniiIIecs
C1dble inlcmII Coaliaua11aS1C1S111e11t mcIhod c.uaillac GD Safety or Medicines Cosl-ulility analysis C'ocOicient or wrilllian Conli.ous wavelel .......... Din:c:lCd acyclic paph Disability alij8led life-)'Car Dlapaal at nnIom DIapauI mmplcrely aI mndaIn DaIa-clepcadcnt Dclipefred Dc:pa:s of rn:cclam DeviaDcc informalion crilcrion
Expeclalion-aaaimilalian
CleIIcraIisc:d Unear mW:cI ..... OcneraIised linear model Gcnaalisallinear mIUcI ...... Gmss ..".aduclion mte
C1enorno-wicla associlllion ·slUdics HcalIh-a4iUSlcd lire cxpecllUlcy Hidclen Markov model Hilliest (IOIIaior·dcnsity ~ H..... IaClRh elbics conunitlec Hcallbcllllcd qualily or lire fclenlily-by-clesc:cal IDlradus (or inIIaclustcr) com:laIioIa cadIlcicat
ICER ICH
~1I1CIIIaI CDII-clra:liveaess ratio InlcmalioDal ConrCRnCC GD
Hannaaizali_
IQ
rrr IV
KDD
laslilulianal .mew board InlcnlioD-~
lllslnanallal variabIc ICnowlqe cIisccway ill clatabuel
KM
ICaplan-Meil;r
IcNN
k-ncan:1t aeilhbaur u.. discrinainanI ftIIIcliDn
LDF LR
LREC LS· LST
MA MANOVA MAR MeA MCAR
~11IIio
Local n:aean:b c:lhici c:ommillee Lcasl·.._ l.aIp simple IriaI MoviI1l awrap MukiWriate ...., . or variance Missialld mndom Mc:cIiciael ConIIvI At,crrl:y
Misslnl. mmpIctcly aI. raacIam
xxi
~~AND~
______________________________________________
M.m. cliaiD MoRa.: Carlo
M~·_·~.~ PnJducis·
.RepIalDay Apacy . M~m_ JikemioacI CIIIinuiIe _ (- C8IimalicIa)
MREC
Mulliccalre ·lUCarch ethiCs caaunillee
MsB
Mc.a.1IqUIR e~
MTQ
MliXim .... Iolerali:d .. . . cloSe Manozyplic: ~ (arnoninfanaalhe)
MZ NI ~.
·:Ncl mcmeIaIy ~ftt.
NNH NNT
.NulDJM:r .aated·IO.hann Niam....... lOlMat Ncpii~ pmlicii~ value
NPV
NUs
Mdt .OLS QR
PeA
PDP PEsr fGM
ftl
.0Idin.y: inst sipuua ·Odds,.aio -PriDciplil companc:al.
anal,. ......,.litY "'Y runciIa. ...... ad B.arian of ~~(IOft~D)
,..,. ~ nicuuni . .
Quanlitali~ .lloci
RCT· REB·
bndomIsed conIIOIIaIlriai Rc~.I.~ .
RBML,
llcscaIda.eIhics cammilleC b ..... max_UIII. UbiihOOd
·ROC·
~eaciwropifttiq ~
ROt
~_ofintaat
RPW
~isacl play~. . .
•• SSM
·S8.t
.SPRT
.SS
,S8
·TDT
PnIpOrtiDaaI . . . .
POP pp
.,. .,...,col·
p'-p
~.JlCl'CCntile
• • • 1~ . . . ~H~t7. . . . . . . . . .
pn,bability
.
.1M
Tail
n·
VAS
wLSi!
~n-·;miIl ~hiJit , .r-" l"" ........ Y c.
Positive paalic:live ·alae
~
Quiaai~1IIlIiIe
.~
SVM
PIiarwnac:oJci_:-.....lo_ _- - - ' - _ : -
PPV
Quality or lire
SMR
PKIPD ppp.
QoL
.SD !S.
' . '
.
~ty. ad)i~ ure:-~.
RR
Naiiaaal Racan:h ElJiic:s . . . .SerVice . ·Net . . . .1CtiDn . .
-~miit
~Y·
RcIaIiWJ
.Ii*
SIancIanI deviation SI8nCIanl~
_ur81 slanclaidi.d
slIuIdIud ciJcr .Of'the mCan;: ~
DDIcJ
l'IIOIIIiIily. raIio . S.aultical parameIric nap psababilily tcit . .ratio .
Seq..,."
SUmofsquans
.
Sum of.squaR:S ~ 10 error s~ -reCtor madu_
TransmiisioD dlsiciltiDn lest· 1bbiJ. fertility rata . ·~rncihod
TiiquIar rat aDaJOpe...Je . W~ .... squan:a estimate
Y"""
(or lIati~)
A accelerated factor
See SURVIVAL ANALYSIS
accelerated failure time models
See Slm1\'AL
ANALYSIS. 'JRANSRlStAnON
active control equivalence studies The classic ranclomiscd aJNICAI.TRIAL seeks 10 prove superiorily of a new lmItmenl to an existing one and a successful conclusion is one in which such proof is clcmansll'alcd. The famous MRC trial of slIqJIOmycin is a case in poinl (Mc:dical Research Council Streptomycin in 'lUben:ulosis liials Committee. 1948). The trial concluded with a signiftcanl difference in outcome in favour oflhc group glven streptomycin compared to the group that was noI. In n:ceal yc:an., however. there has bcc:nan iDCMaSing inletat in IriaIs whose objeclive is to show thai some new therapy is DO worse as repnls some outcome than an existing treatment. Such trials ha\'C particular featwes and difftc:ulties that wen: described in an important paper by Makuch and Johnson (1989) in which lhcy used the term 'active control equivalence studies' (ACES). Actually. lhc term is nul ideally chosen since. unlike bioequivalence studies. when: Ihe object is to show that the bioavailability of a new formulalion is not only at least 204Jt less than that of an existing formulation. but also at most2S 4Jt more, ad he:nce w~ f!qUilYllence 10 some dcgn:c: is genUinely the aim, in ACES it is almast always Ihe case that only noninferiority is the goal. II may be questioned as to why the: rather modest goal of noninferiorily should be of any inlclal in drug regulation. There arc several reasons. 11Ic flnt is lhat the new drug may have advDDtagcs in lenns of tolerabililY. Second. the new drug. while showing no net advantage to lhc existing one. may increase patient choice and this can be useful. For example. many people have an aspirin allergy. Henee. it is desinble to ha\'C altcmalive analgesics, even if no better on average than aspirin. Third, it may became necessary to withdraw tn:abnents from the market and one can never pR:dicl whe:n lbis may happen. 'I1Iere IR now several stalins on the market. 1be facl that lbis is so means that withdrawal of "riYaSlatin does not make it impossible for physicians 10 continue to treat their patients with this class of drug. Pourth. introduction of further equivalent therapies befon: patent expily of an innovator in the class may pennit price compelition to the advantage of reimbunors (although such competition is probably not particulariyeffccti\IC; Sean ad Rosati. 2(03). However. the nOh nmon is probably the most important Dnq; regulation is designed to satisfy some minimum requirements for phar&qdOfNllldjt CtNHpIIIfioIr It) Mftd"1IYI1 Slalislia; S«rMd EdiliufJ C 2011 JohD Wiley & ~ ....
maceuticals: that they are of sufficienl quality. arc safe and emcacious. Efficacy isdcmonstrated iflhc treatment is better than placebo. even if it is not as good as some other treatments. The comparison of a new drug 10 an active In:alment may be dictated by ethics but the object of the trial may simply be an indin:ct pRlOf that the treatment is beuu than placebo through ClOIDparison to an agent whose emcacy is accepted. Rctlently the issue of the indirect comparison to platlCbo has been taken more seriously. Consider Ihe cue when: we ha\IC a single effectiye treatment on the market, say A. whose emcacy has been demonstrated in a series ofbials comparing ilto placebo. We now run some new trials comparing a furtha treatment. B. to A. 1bking all these trials together, they then have lhc structure of an incomplete blocks design. The effect of B compared 10 placebo can then be estimated USing Ihe double contrast of 8 comparai 10 A and A compared to platlCbo. This approach has been examined in detail by Hasselblad and Kong (2001). A CXJIIscquence of taking this particular view of malleI'S is that the precision with which the effect of A was established compared to platlCbo cannot be excec:dc:d by the indirect comparison of B to placebo. since the variance of this indirect conlnSt is the sum of Ihe variances of the two din:c:l CXJIIlraslS. This is. however, nol the only difficulty with such studies. The folloWing are some of those that apply.
Est.liming Q cliniCtlIl,. irrelevant difference. Ifthe route of a fannal anaIysisClOlDpamd 10 placebo via an indirect contrut is taken. this particular difficulty may be finessed. Tbe new RalJnent is shown to be 'sipiflcantly' better than placebo. albeit using an indiru1 argument. and the extent of its inferiority 10 the campanlOr is only of relevance 10 the extent that it impinges on the proof of el1icacy compared to placebo. If this proof is provided.. then the comparison to the actiYe compamtor is 'walei' under the bridge' . If this particular approach is nol taken. howcvu. lhen any proof of eflicacy of the new tn:atmc:nt rests on a dcmonslrlllion that it is not 'substanliaUy inferior' to the CompandOr. which camp;uarar is accepted as being cfftcacious. 1bis nises the issue as to what it means for a ckug to be not substantially inferior to anolhcr ODe. This appears to rcqui~ that some naargin .d • .:I> O. be adopted such that if" is theelllent by which the new trcaIment is inferior to the slandard (where r < 0 indicates inferiority) then it is judged subslanliDlly inferior if 1" :5 -.:I and not subslantially inferior or "equiYalent' if T > -.d.
Edited by Briaa S. Everitt and ChrisIGph« R. P'dmeI'
1
ACTIVEOONI'ROL EOUIVALENCE STUDIES _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ __
Tecl",;clI/ slolislim/ IDpeds. In a Neym~Pc:anoD hmewarlt (sec Salsbury. 1998) the lesl of noninfcriorily raauira one to use a shifted NULL HYPOrHESIS. One miPt. thcn:fon:. adopt Ho.~~-A. The silaalion is DOl lIS canlnn'asial as thai for InIe biacquiyalence. where the fiact thai two hypotheses have 10 be rejected. that of inferiority and that of superiority. means that an inlaiU", approach of seeing thai the confidence limits for the ditreraace lie within the limils of c:quivalc:ace is not 'optimal' (Beller and Hsu. 1996~ althoUlh the 'optimal' lest may in pnldia: be: worse (Perlman and Wu. 1999: Senn. 2(01). In praeticc. in the case of ACES if the lower CXlDYenlionai I - a ,wo-sided CONFlDENtE INIBlVAL for ~ excc:cds -A. Ihc hypothesis or substantial inferiority may be: n:jcclcd .. the level a ad noninferiority asserted. n might be: thoughl that a o~sided conficleace inlCrVal would be suftlcient for this purpose. Howc:Yc:l', the general rqulalory CXlDYenlion is Ibal all tests clc:signed to show superiority an: lwo-siclc:cl (despite appan:nt purpose) and. since such tests an: a special case of a noninfcriorily lell with.d =O. usc or onHdcd tests for noninferiority would lead to inconsistcncies (Sean, 1997; Committee for Prapric:bUy Mcclicinal Pnxiucas. 2000). In a Bayesian framework (sec BAYESIAN .IEIHODS) one might RqUin: that the posterior probabilily of noninferiority wen: less Ihan same specific:cl amounl. Abanalivcly. use of a loss functian would permit a clcc:ision analytic meIhod. such as has been proposed for bioequiva1ence (Undley. 1991). to be used.
Po...~r of ,rio/£. Nole that the rcasan one daes not employ a value of A = 0 in practice is that unless it is expected that the new ImIImeat Rally is better than the slandanl. the power of the resulting test could nevc:l' exceed SO fJ,.
However, the clinically im:levant difl'cn:nce is likely to be less than the clinically n:levanl difl'en:nce used in CXlDYentionalliiais. Hena:. if the new tn:aImcDt is ac""'ly no bc:_1han the stanclanl IRalment. then. for a given sample size. the IIOIICICntndity panamcler. cl == AISE(J) is likely to be: smaller f... ACES than for lliaJs designed to show superiority. COIIICqucntly. ACES either have lower power ... higher sample sizes than conyentional trials.
A.uay :lensili"ily. A pmbIem with ACES is thai if the trial appears to show noninferiority or the new IIQtmcnt. then then: are thn:e plausible explanations. 11ac lint. thai of cluance. is one: that statistical analysis is designed to addn:ss. 111e second. that the new IIQtmcnl is indeed noninfcrior. is what was dcsimlto prow. However. a thinl possibility. that the experiment was not sensitive 10 find a dift'cmacc. is difficulllO exclude. "111 is issue bas been n:rcm:d to as anc of ·competenc:e' (Senn. 1993) and atrects whalc\'CI'
infcn:ntial framework one decides 10 usc. An analogy may be uscrul hc:rc. In a pme of hUnI the thimble. a found thimble renders the quality or the Slrately used for finding it irrelevant. II is no marc 'found' ir a goad stnIcgy wen: used than if a bad ODe were. However. a failun: 10 find a thimble docs not automatically justify the conclusion that the room doc:s nat contain one and the quality of the SCBIdI employccl is a CI1ICiaI consideration in any judgemenl that it doc:s noL
TIre ejfed of DROI'OU1S, NONCOJIPUANCE tmd lire role of tnltllysu. It is plausible that in many cin:UJI1Itancc:s in conventional superiority trials if IICIIICOmpiiana: 01' clmpauts an: a problem an intcnlion-l~ IRat analysis will give a more modest estimate of the IRllllllcnt effecl than will a PER PIIOMCOI. analysis. In ACES. it is at least plausible thai this may nat be the case. INTEN1ION-ro-TIlEAT
COIfjlid ojrequiremenls ofodt/ilil'/Iy IIIfdclinical re/eFtlllt:e. It may be that the clinically irrelevanl diffen:nce is most meaningfully established on a scale that is nat additive. For example. in a trial of an anti-inrective. it could be most appropriate tocstablish thai theditrerenc:e in cun: rate an the PIObability scale was DOl gJaIIuthan lOme specified amounL Contrariwise. the log-odds scale mighl lend itself marc n:adily to staUstical modelling. This can lead 10 consich:rablc climcullies (Holmgn:n. 1C)g9). in panicular because a trial doc:s not Rendt a nmdom sample fmm the lalgct papulation. It may be that funhcr modelling usinI additianal data may be necessary (Sean, 2000). A CGIIUIIOft ein:umstana: likely to make n:gulalOly authorities ask questions is that a trial thai was designed with optimism to show superiorily to an active co. . . .t... fails to do so. but then is used 10 aIIc:mpIto dcmonstndc noninfaiorily. 11Iis parlic:ular set of cin:umstances has bctvmc Ihc subject ofoncofthe European Medic~EvaluatiaD Ageacy's 'poinls to consider' (Scan. 1997; CommitlCc f... Proprietary Meclcinal Pmducts. 2000). This stresses the desirability of elilablishing the trial's purpose prc-paf'armanoc and also warns apinsl establishing the clinically irrelevanl diffen:ncc. A, after the trial is ClDIDplcte. II ~ putlinl a trial thai was designed to show superiority to the puI'JJCl5C ofncminfcriority as an unac:a:ptableusc butKCqJtstheconvcnc.111e guideline recognises thai then: an: no issues of multiple Ic:sting involw:d with such switches (Bauer and Kic:sc:r. 1996) but that establishing values of A mraspc:clively may be biasing. 111us. it is preferable ror invcstigalOlS to specify in adwncc (e.g. by mcansof fannal chanp to the QlNlCAL TRL\LS JIIOIOCOL) Ihcir inlenclcd switch or purpcI5C and to nx the yalue of A prior 10 data unblinding. This. however. raises the ilSUC as 10 whether
______________________________________________________________ ADAPnVEDESIGNS the value of.d is not somclhing the regulator shoulddeclarc for given indications rathcI' than relying on the sponsor to do so. Otherwise,. a regulator could be raced with the following position. Drug B is rqislcnXl on the basis of comparison to a standarclln:allnent A bc:c:ause the lower confidence interval ror the lrealment effect. TIJ_A' excc:eds same pre-spccifted ,·a1ue..d. HoweVCl', a further drug. C. which has also been compared to A, is notgranled a lia:ace because a superiority trial was planned. Although superiority to A was not proven. the lower confidence inlerval for the In:aImeni etrc:ct 1'C_A excludes a smaller possible ditT~1It'e between C and A than is excluded for the difference between B and A by the lriallhat has led to rc:;istralion of B. SS B...... P. aad Kieser, M. 1996: A urufying appRl8l:h f«confidence inlm'als and testing of equivalence ud difremICC. Biometrika 83. 4. ~7. . . .r.1t. L aad Bsa. J. C. 1996: Biocquivalcnce mals. intcrscClion-union ICSts and equivalence confidence sets. Slatiftical Sdenre II. 4. 283-302. CeaualUee for ProprIeWJ l\IedldaI Prodad.s 2000: Points to oonsider on Switching between superiority and non-inrcriority. HUllibIad, V. aad 1CoDa. D. F. 200 I: Stati.stkal methods ror compcuiscn to placebo in acliveoCOiD)1 SlUdies. Drug In/ormation Jorunttl35. 435-19. RoIIngreD, E. B. 1999: Establishing equivalence by shwing that a speciftcd perce8IagC of thc cffect or the active control over placebo is maintained. Joumal of BiDplrarmat't'llticalStalisti(,..J9.4. 65 1-9.IJndI..,.. D. V. 1998: Decision analysis and biocquj\'aJcncc lrials. Slatisim Sri~lfCe 13.2. 136-4J. Makudl, It. aad Jabasaa, M. 1919: Issues in planning and interpming adiYe control equivalence studies. Joumal of Clinical Epitlenriology42. 6. 503-1 I. MedkaI Researdl CoaDdI sa.... m)'dn III Tabercu1a511 Tdais CGlllllllttee 1948:
~ptomycin
batment for pulmonary tubcmalosis. Brilish Medical JoufIJQl ii. 769-82. Pedmaa,M. D. aad Wu, L. 1999: 11ac empeRll"s nc\\' tests. Slalistical Sciencr 14.4.355-69. Sal....,., Do 1998: Hypothesis testing. In Armitage. P. and Colton. T. (eels). EnC)'tiopedia of biDslatisti('s. Chichester: John Wile)' & SOlIS. Lad. Sea&. S. J. 1993: InbaaIt difficultics with active control equivalence studies. StalUtia in MeJitUre 12.24,2367-75. SeDII,S.J. 1997: Slatiftical ismr.f in drug tlrvelopnrent. CUchestcr: John Wiley & Sons. Lad. s.m. S. J. 2000: Consensus and con~ny in phaimaceutical statistics (\\ith discussion). 1M Stalistician 49. 135-76. Sean. S. J. 2001: Slalislic:al issues in biocquivalencc. StDtiftia in Medidne 20. 17-18. 2785-99. Seaa. S. J. ad ItaIad. N. 2003: Editorial: Pharmac:eutic:als. paIcnIs and competition - some stalislical issues. Joumoi 0/ lire Royoi Stalislical Sot'iel}' sma A - Statisti('s in Sotiety 166. 271-7.
adaptive designs
a.JNJC\L 1RLWii that arc adapli\'C arc
modified in some way by the data dud hayc aln:ady been collected within that trial. The most common way the designs adapt is in the allocation of treatment. as a function or the n:sponse. For example. we may be interested in a dose that givcs a 20., chDlKlC of toxicity. whel'CCX"SSCS to this level of toxicity would be harmful. Thcrcrol'C, we may want to design the trial in such a way that. as more infonnation is gath~d. doses are a1loealed to optimise lhc estimate of Ihat dose.lfwc
were to usc a traditional fully nmdomiscd approach to runnirq; the trial. which is not adapth-c. we would probably not look at the data until the end or the trial. thereby risking exposing subjects to toxic doses and also possibly failing to produce an optimal estimate of the RXluired dose. Another such example of an adaptive design isgival in Rosenberger and Lachin (1993). whereby there arc two trcalments in the study, A and B. and as inrormation emerges from the triaI.he treabncnt assignment probabilities arc adapted in an aucmpt to assign IDOI'e patients to the treatment pc:IftXllling beucr thus far. 11Jereforc. when a patient enters the study. ir treallnent A appears to be better than treatment B, a patient has a greater than 50 Cit chance of being allocated In:alment A - and vi" vena. Because adapti"e designs modify the allocation of treatment on an ongoing basis, and thus protect patients from inefTeclive or toxic doses, they can be said to be more ethical than traditional designs. Rosenberger and Palmer (1999) consider the ethical dilemma between collective and individual ethics (see mucs .~ND CUNlCAL TRIALS) and argue thai in a clinical trial setling indh'idual ethics should be uppennosl; i.e. consiclendion should be towards doing what is best ror patients in the current trial as opposed to doing what is best for future patients who stand to beneftt from the l'Csults of cUlTCnt trial. The Declaration or Helsinki of October 2000 outlines the tension between these two types of ethics by stating: ·Considerations related to the well-being of the human subject should take prcc.x:dence over the interests of science and society: It is adaptive designs thal address the indiYidual ethics, as opposed to fully randomised designs. which address those collective ethics. We will be dealing primarily with n:sponse adaptive designs here. such as those just outlined. and will not be describing those designs that atlempt dynamically to balance the randomisation forcovarialc information. such as oUllined by Pbc:ock and Simon (1975) (see D.~TA-DEPENDEHT DESIDNS. MJmMISA11ON).
The randomised play winner (RPW) design attempts to a1loeale trcaIments to patients sequentially based on a simple probability model. Rosenbeq;er (1999) emphasises that the RPW design speciftcally applies to the situation whel'C the outcome from a trial is binary, i.e. either 'success' or 'failure' and where there arc only two lrealments. e.g. chug A and drug B. At the start of the trial there is an assumed urn of a baDs of type A (which rehde to drug A) and fJ balls or type B (which relale to drug B). When a subject is recruited. a ball is drawn from the urn and then l'Cplac:ed. If the ball is type A then the subject is allocated to drug A. if type B then the subject is a1loeBled to drug B. When the subject's outcome is available (and we assume that the outcome is available befol'C the next subject is randomized), the WD is updaacd. If the response is a success on drug A.then a ball ortype A is put into the urn, and
3
ADAPnVEDESIGNS ______________________________________________________________ similarty fora success on drug B.lfthe ouk:omc is a failure on drug A. then a ball of t)'pC B is put into the urn. and spin similarly for a failure on dl1ll B.ln this way. the balls build up such thai a new subject has a better chance or being allocated to a better lreatment. Rosen~er (1999) concludes with a table of eonditions UDder which the RPW rule is reasonable and provides a rQlistic allenlalivc to the standard cliniul trial design. These an: given in the table.
adaptive designs CondItions under which the RPW Is reasonable (Rosenberger, 1999) • The therapies ha\"C been evaluated previously for toxicity • The raponse is binary • Delay in n:sponse is mociemte, allowing adapting to take plaee • Sample siza an: moderate (at least SO subjects) • Duration of the lrial is limited and recruitment can take plaee during the entire trial • The trial is carefully planned with extensive computations done under dilTerent models aDd initial urn compositions • The experimental therapy is expec:led to have signiflcanl beneftts to public health if it proves effective
Traditional dose-n:sponse studies. where patients are allocated to a limited number of doses along an assumed dose-rcsponse cun'C. are limiled and. some would say. wrong. For example. if the assumc:d dose-n:sponse model is inCOlTCCI then palients may be allocated to ineffc:cli\"C or unsafe doses. One answer could be to increase the number of doses. However. this would resull in many patients allocated to wasted doses. It would be much belter 10 increase the number of doses and allocate doses to a subjC:CI based on cum:nl knowledge of the dose-response curve. which best optimises some IR-spc:cified criteria. This is precisc:ly what Bayesian response adaptive designs attempllo do. by employing Bayesian DECISION THEORY to a utility function. Thus. the dose thai most optimally addresses the utility is allocated to the next available subject or cohort of subjects. One of the first BA~ r.tE1lIDDS described was the continual mlSsessmc:nt method (CRM), inll'Oduced by O'Quigley. Pep.: and Fisher (1990), and originally devised for dose-escalalion studies in oncology. Whitehead el QL (200la) suggest that the method ClOUld also be used for applications in other serious diseases. The CRM c:nvisages a study whereby human voIunlc:ers are lrealed sequentially. in order 10 detc:ct a dose with a probability of loxicity of 20 CJt. i.e. TD20. The ~sponse is a binary response, 'Ioxicity' or 'no toxicity'. Before the study staIts, investiptors are asked to proVide what their best guess is of a probability of toxicily at
each or the series of doses. The first patient is then ~aIcd with the dose that is aJllsidcred to be the closest 10 the TOlD. Once the OIIk:ome is obsc:rved the FROB.o\BlUTYof Ioxic:ity at each of the doses is recalculaled using the Bayesian method of statistics. The proccd&R continues in this way until it wtles on a single dose. Whitehead el QI. (2OOIa) point out that the CRM does home in 011 the ro20 quickly and efficiently, but then: has been concern that early on in the lrialsubjc:cts could be allocaled 10 too high a dose. leading 10 palentia) toxicity problems. This has led to a number of modifications. such as starting at the lowest dose and never skipping a dose during the escalation. Whitehead el aL (200lb) suggelil practical exlensions to the CRM for pharmacokinclic data. employing the use of Bayesian decision theory 10 allocate ~alments optimally 10 subjects. They argue that conventional dose-escalatiOll studies carried out in healthy volunteers do not normally employ statistical methodology or fonnal guidelines for dose escalation. As such the studies can take a long time 10 complc:lc with little opportunity to skip doses. The methods proposed allocate doses in anlcr to maximise the information about the ~response curve. gi\'Cn a pre-speCified safely constrainL They use two simple utility or gain functions. one that allocates the highest allowable dose under the safely constrainl and the other that allocates doses in order to optimise the shape of the dosc-n:sponse curve. Krams el al. (2003) also use a Bayesian decision theory approach with sc:quential cIase anocation 10 a Phase II study in acute SIroIcc therapy by inhibition of neutrophils (ASTIN). which employs up 10 15 dose levels. They usc a responseadapti\"C procedun: in order to find a dose that gives an improvement over that of placebo in the primary ENDPOINT. allocllling the next subject eilhu to the optimal dose or FLo\CEBO. Slopping nales were employed by which if the pD5lerior probability of an effectivc drug or ineffective drug were greater than 0.9 then the dc:cision would be made eithu 10 go on 10 a confinnatory lrial (effeclive dnag) or to stop development (inelTc:ctive drug). In this way. they were able to stop dc\'Clopment or a compound more quickly than would have been possible under the traditional panuligm. In 2006. the Pharmaceutical Research and Manufacturers of Amc:rica (PhRMA) Adaptivc Design Working Group pUblished a series of papers in an issue of the Drug Information Association (DIA) joumal detailing various aspects of these lrials. Topics included terminology and classification: implementation; conftdentiality and trial integrily: adapti\"C dose response: seamless Phase IIIIlI: and sample size n:estimation (see Drug In./OTnJlllion JOIImal40. 425-84. 20(6). In addition. and re8ecling the growing inleresl in adaptive designs. there have been numerous special editions of other jounaals devoted to these trials. includi~ JoumQI 0/ Slalislical Pltllllling ad In/erence. issue 136(2). 2006: JOUTnQI of BioplwrIPlQt:eUliml Slalislics. issues 16(5).
_ _ _ _ _ _ _ _ _ _ _ _ ADJUSTMENT FOR NONCOMPlIANCE IN RANDOMISED CONrROLLED TRIALS
2006 and 17(6). 2007; and Stalislics in Medicine. issue AS
27(10). 2008.
KnIll., Mot Lees, JC., IIac:b, W., Grine. A. p.. Oraoaau,J..l\oL aDd Font. O. A. 2003: Acule IIIakc therapy by iabibilian of nculnlphils (ASTIN). An adaptive cIose-Iapoasc study or UK279.276 in Kute iscbanic stnIke. SlroJcr 34, 2543-8. Paeoek, S. &ad SImaa, R. 1975: ScqueDliaillatmcnt assipmeDl with ~ iltl or prolDDSlic factCIIS in CGIdIOllcd clinicallrials. Biome"k~ l I. IOJ-IS. O'QaIIIe". J., PIpe, Me aDd FIIbIr, L 1990: Coalinual reassessment mcIhod: • pl'ldieal design far fhasc 1 clinical trials
in cancer. BionretTia ~ 33-11. _ ...... W. F. 1999: R..cIomiJJCd piay-lhc-winDc:r clinicallrials: rmcw and m:onuneadatians. COIIIroil. Clilriml Trab 20, 321-12................ W. F. &ad tar..... J. M. 1993: n.e usc or rapanse-adaptive designs in clinicallrials. Co""oIledClinimlTrillh 14. 471~............., W. F.... hIBler, C. R. 1999: Ethics 8IId practice: alternative designs far Phase 10 ranclamised clinicallrials. COIflrollfti Clinical Triola 20, 172'-. WUeMad, J., Y......... z., P......... So, We""", D.... Fraadr, S. 2mla: Easy-lO-implemcat Bayesian methods far dasc-esc:alalian studies in healthy volunteers. Siolla· lirl;cr2.47-61. WMtebead,J.. ZIIDa, y ..staIIard,N..Tadd,S. ... WbIIeIIad A. 2OO1b: Lamial fram JRYious responses in Phase 1 cbc-esc:aI.oa 1lUdics. BTitUir JDIInIIlI of ClininrJ Pbsrnlll(,o/ogy S2. 1-7.
aon
adaptive rancloml..
Sec ADa\P11YE DESlCINS.
JlANI)CaUSATlON
adJU8Imeni for noncompliance In randomlaad controlled btala In clinical medicine. ·noncompliance' occurs when a patient does not rully rollow a prascribed course: of lIaImenL The alternative terms "adhcmlcc' and "concanlance' attempt toaw.icltheautharilarian cwertonc:s or "compliance'. In randomisecl QINIC'AL TRL\U. we an: cancemc:d with any ~ rrom a randomisc:d lRalmcnt. whether due to noncompliance CJI' a In:alment change q~ed with mc:cIical staff. In a trial to eamlNR two types or medication (drug A and dnag B. say) for the: tn:aImeat or hc:art disease. far eumple~ patients may ~ftlse or rorgc:t to take any of their medicalion or £orgc:a to Iakc: it some or the time (partial compliance). PatienlS aliocalcd 10 ra:cive dl1lg A might switch to drug B~ mad vice versa. Some of the patients mayevc:a take anaIhcr mc:dication altogether (drug C. say) or. particularly ir the Ihcrapy appears to be failing. RXlCive a much more radical intc:r'VCntion such as surgery. A rwther complication for the estimation of In:aImenl effects arises when patients who fail to comply with thc:ir prescribed tratment an: also Ihose who an: IIIIR likely to be last to follow-up.
Ratiollllie. Conventionally. trials with c1cpanun:s ftvm mndomisc:d tn:atment lire analysed by IN1ENI'JON-~TREAT. This clim:lIy compares the e;8'rclirmess of the diO'e..,nt
In:abnent policies as actually implemented in the llial e.g. "drug A plus changes' venus ·dlUg B plus changes'. Unlilcc efl'ectivc:aess. f!//k1lC)' ..,11lleS 10 the eITects or the In:alments themselves. and is not estimatc:d by an intc:Dtionto-trat analysis.. Rc:scan:ben may also be inlclated in the: eO'ectiveness oran intervention in othc:rcilaunslancc:s. e.g. if public suspicion of the intervention had bec:a ~duced by the positive aawls of a clinicallrial. In these circumstances. the: ratc:s orcompliance may be improved and actiustment for this change may be aIlc:Inpted. It is imponant to define the aim or adjustment for noncompliance. For example. in a trial of immediate venus c1crc:nat zicIovudine in asymptomatic HIV infc:ction. the: initial plan was to derer zidowdine until the onset of symptomatic disease. However. rollowing a pnJtocol amendment. some individuals startc:cI zidowcline beron: the onset of symptomatic disease (White et Ill.• 1997). Then: was interat in estimating the eITect Ihat would have been absc:m:d undc:r the original protocol. Zidovudinc: beron: the onset of symptomatic disease was thc:n:rore regarded as ·noncompliance'. Other individuals stopped zidovudinc Imdmc:IIt because of advc:rse events. Additional adjustment ror stopping tn:almc:nt would not answc:r a clinically relevant question. so the analysis did DOl aim 10 estimate efficacy. Adjustment rar noncompliance: is useful in a variety of situalions. Patients may be most intc:n:sIcd in In:alment efticacy. DiO'e~nc:cs in compliance may help to explain variation or a lreatment effm with time. between subgroups in a Irial or betwc:c:n trials in a .mAo-ANALYSIS. Reconciling llial daIa with obscr'Vational data may laIuire adjustment rar noncompliancc: in the: trial. Policy analysis may lellui~ projc:ctions for situadons with improYed eampUancc:. Most llllempls 10 allow ror noncompliance use on-IRalment analysis or PER PIIDI"OCOL analysis.. This only proviclc:s a valid comparison of the In:alments themselYc:s (efflcacy) if complic:rs and noncomplien do not cliffeI' systematically in their disease stale or prognosis. In practice this is unlikely to be the case. so selection bias occurs. Heart clisc:ase palic:nts who comply with their pn:scribc:cl medication. rar example. 1ft also those who an: likely to impro~ thc:ir diet or lab man: exc:n:isc and thesecllanges. in lOm.1Ire likely to lead toa better outcome. SELECTION BIAS may often be n:duced by adjustment ror baseline m\'ariates~ but thc:n: is still no guanntcc of an unbiased analysis. For elUUllple. in the: Coronal)' Drug Pmjc:cl. 5-year manaUty of poor eampUc:n was 28.2 CJt compared with 15.1 CJt in good mmplic:~ and adjustment far 40 baseline ractors only raIu4"ed the diITerence to 25.8 CJt vc:nus 16.4 CJt (The Coronary Drug Project
Rc:scan:h Group. 1980). Newer ·randomisation-basecl' methods am estimate emcacy while aw.iclinl selection bias by din:dly comparing the groups as randomiscd as in an ination-IO-tn:at analysis (While., 20(5). This is made possible: by considc:ring the
5
AGE-PERIODCOHORTANALYSIS _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ __
subpuup or 'compliers' who would ha\'e n:ceivcd Ihcir mndomised batmen.. whichever group they \\'ere nndomiscd to. For example. a trial in Indonesian childn:n campan:cI vitamin A supplemc:alalion with no inlerVention. the outcome beil1l 12-month manalily. Vitamin A supple. or the intervention ann and by DOlle or the caatnJl ann. Sammer and 2qcr (1991) cansideml the subgroup who did not n:ceive vitamin A in die intervention ann and a corn:spondilllsubJrouporlhe conbol ann who ~·ould rrol/raJ,-e ,eaiJ,-eti l'ilanrin A if Ihey bad hem allocaled 10 receire il. These 'noncomplier' subgroups were assumed to be unalJ"ecled by allocalion to vitamin A. It is then straiplfolWani to estimate abe number or nancomplic:n in the conlrol arm and their mean outcome. and hence the risk difTen:ace. risk maio or odds ratio in complien. This is oRen called the 'complier .~ causal effect' (CACE) estimate (Utile and Rubin. 2000). This approach is • special case of PRINCIPAL STRAnFlCAtICN. A man: gc:aeral approach requires a model n:laling polential oUIcomes for each individual under different caunterractual In:almc:ats. A simple model mipt sa)' that each individual would have blood pressure b nunHg lower if they lOok abe cIru& with perfect compliance than if they did not take the cInas. with pmpodional blood pn:ssun: mluclions for pallial compliance. Such • maclcl may be lilted by abservil1lthat untn:ated blood pn:ssure must have the same dislribulion in each rancIomisc:cl group (Fischer-Lapp and 0adJhebc:ur. 1999). An important ad\'8Rlage of these methods is that no assumption is rcquin:d about the relalionship bc:Iwc:c:a compliance and polc:IIliai outcomes. 'I1Iey are closely related to the use: or JNSTIt1}),IE1Il VAlUABlES mdhods (Dunn and 8entall. 2007). The approaches just described are genc:rally only able to estimate one tn:almenl effect in a Iwo-ann trial. They ad to be: hopelessly impra:ise: in situations such as EQUIVALEICE STUDIES where patic:ats may Slopallbatment during the trial. so that the analysis rcquin:s estimation of the elrect or both lIaImenlS.ln this case it is possible to adjust abe nndomised comparison usil1l observational estimation of one or more treatment elTects - i.e. assuming the~ are no unmc:asun:d caafounden for tn:aIment. Methods such as mtlrginlJ/.rlnlcIliral modellirrg can work e'VCII when at'tuaillalmeni is both a consequence of symptomalic deterioration and a cause of slowa' disease progression (se:e Little and Rubin. 2000. for ~ferences 10 this literalUre). A trial wilh noncompliance has less POWER than one with perfect compliance. as a n:sult of Ihc mlUClCd effect size as estimalc:d in an intcDtion-lO-Rai analysis. and it is natural to want to n:cover the last power. Howe~r. many or the DeW pnx:ed1RS preserve the intcntion-lo-Cn:aI SKOOF1CANQ LEVEL and thererore do not affect power. In some cases. il is impossible to relain power without makil1l some assumption mentation was actually received by only 8Oe.t
abaat comparability or noncompliers and compliers. In athc:r situations. some gain in power is theoretically possible. but this is unlikely to be appn:ciable in plKticc (Becque and White. 20(8). Signiftcance testing should therefon: rely on intention-to-lmll analysis even when other melhacls are used to estimate emCat'y. IWIGD
w.....
AnpIst,J. Do, IID....O. RaItIa,D. B. 1996: ldentificlllioa of causal effects usiq illSlnllDeDtal variables (with discussiOll). JoumaloJlbe AmtriamStaiinicalAs.ftJdalitHI91.~72. B....e. T."'" WIllIe. L R. 2008.ltepininc pG'A'Cr lost by non-campIiance via full proIIability modcllinc. Slatistiu in Medicine 27. 5640-63. DulIn. G............. R. 2007: ModdlinglJatmcnt-cffc:ct hcaem~ity in rancIamizcd CGIdIOllcd trials of complc:x intcnentiaas (psydlolCJCical tn:aImcnlS). StaiulicJ in Meditillt 26. 47(4)....15. .....-....." K. .... ~.... B. 1999: PmcticaJ pnJpCrties of same structural mean analyses of the effect of compliance in
randomized trials. COIrtroiletl CliRitll' Triu& 20. S31-46.1..1tt1e. R-
.... RuIIIn. 0. B. 2000: Causal effects in cliDical and epidemiological studies via potential oukClmC5: CCJIICCIIlS aad analytical a~ praachcs. A""""I Bern· oj PIIbIir Health 21. 121~S. 'Ibe C..... ..,. Draa PmJtd R..ardI Graup 1980: InIIueaoe of adhaaace to lRallllent and rapoIIle 10 cholcsaeml on mortality in Ihc CORJRII)' Drug PIojed. Nn' Eng/ad./tJumQ1 tJj Akdkine 303, 103s-J1.
WIllie, L R 2CJ05: Uses aad limitations or randamizaIioa·1Jascd eflicaty cstilDldol5. Sialislital MellrDt/s in Medial' Relml"ch 14,
327-47. \\'Idte. L It, Walbr,5..BaIIIker, A. G...... .,.,.,......... J. R. 1997: Impad of tn:abncnt chanFs OD the inlcrpmaaion orthe Conconle trial. AIDS 11. 999-1006.
.ge-perlocI cohort ...lysls
To understand die effect of lime on a particular oulcome ror an individual it is c:ssenlialto n:alisc the n:levanl temporal praspc:ctive. Ale affects mIlD)' aspects of life. including Ihc risk of dise:ase. sa this is an essential componc:at or any analysis of time trends. Period denotes the elate of Ihe outcome and if Ihc outcome varies with period it is likely to be due to some undedyilll fat'tor that affects the outcome and varies in Ihe same way for Ihc entire population under study. Cohort. aJIItrariwise. refers to lencrational effects caused b)' factors that only affect particular &Ie groups when their level changes wi'" time. An eumple ora period effm would be a potential elTecl of an air contaminant thai affected all qe poups in the same: way. If Ihc leyel of exposure to thai fat'tor incrcascdlde.creased with time. ellClting a change in the outcome in all age groups. then ~ would expc:ct • relalcd paltel'll aclDSS all age poups in Ihe stud)'. In studies that take place over IOIIJ periods or lime. the technology for measuring Ihc outcame may change. giving rise: to an arlifactual effect thai was nol due to change in exposure to a causative ageaL For example. intensive scn:ening for disease can identirydisc:asc: cases that would not previOusly haw: been identified. thus artificially increasilll the disease rate in a population has had no change in exposure over time.
"'aI
___________________________________________________ Cohort (also called birth cGbart) eJrcc:ts may be due to fllClorS n:1ated to exposun:s assacialed willi Ihc dale oI'birlh.
suc:b.dIe inlRMluctianofaparticulardrul_pnldiceduriDl dial was bmuchl in at a parlicular point in tilDe. FarexampIc. aprepancy pmcticc assaciated with iDcn:asc:cI risk and adapk:d by the popuIaIian or mothers cluriDg a panicular tilDe pcriodcould aired the risk during Ihc lire. . . of Ihc c:nIiR: ICncnllioa bam cluriq thai period. While it is conunaD ton:l'crto thc:sc: efl'eclSas bc:inlassodatc:d with Jar ofbinh..lhcy could also be: &be ",sak or chanps in c:.x~ thai occ:unalaRcrbirth.ln .....y inclividuals..lifell),le fadexs thai may affect disease risk ewer a lifetime an: Iixc:cI .Ihcy approach aduldlaacl.. Aqullllliftcalion ofthesc cft'c:ctson such a pnc:ndian would give rise 10 a COlDpuisan oflhc:se cohort or ICncndioDaI efra:ls. An inhc:n:nt n:dunclancy'amGIIglhcse thrc:c Icmponl fae. Ian arises rram Ihc facllhat knDwin& any lwo fadon implies the of &be third. Farc:.xaaaple. if we: know an individuals • Cd) at a given date or period, (P). Ihc:n dac: cabart is the difrCIaICC (c =p - II). This linearclepcndc:ncc liYC:Srise to an idc:nliftalH1ity pmblc:m in a fonn" ...-c:ssion model that atlc:lllpis to obtain quanlilali~ c:stimates of rqrasion .,.... mc:Icn lIIIOC:iated with each IalDporai c:1emc:at: pn:p8DC)'
AG&P~ODCOHORT~~S
aenlS or ownIllinear tn:Dd and curvallR ar cIc:paItIft fram I.ar_ In:nd. For c:uaaplc. • can be gi\len by ai i P.. + ci ;. when: i i - 0.5(1 + I). tI" is die overall slape and ;;; the cunalule. The ownIl model can be: expn:ssccI as:
=
=
2010
_lie
E[Y) = flo +II/l. + PIl, + r/J" Using Ihc linear n:latiansbip between Ihc lives rise ID:
~ f~exs
ElY] = Jlo + 4. + p/l, + (P-")Ilt = /10 + d(IJ,,-!Jt) +p(JJ, + /le) 'which has only two identifiable piaramcIcn bc:sidc:s the inlcR:c:pI instead of die c:xpectccl tIRe.. Another way of Yisualising allis phc:aolllCllDll is Ihat all eambinatians or SIC. period and cohort II1II)' be displayc:cl in &be LExIs DIACIWI (_&be ftpn:)~ which is obviously a n:pn:sentaliDn ofa twodimc:nsionaI plaac inslCad of die: tine dimensions cxpc:c1Ccl for tine separate factors. In pnc:nl. dlCse analyses an: IIDllimited to linear cfl'c:cIs appIiccllo a eaalinuous mc:asun: oflimc:~ but iDslead dle:y 1ft applied to b:alporal intervals.. such • disc:aso IIIICS observed for 5- or l~ycar intcmds or.., and period. When Ihc widths of these iatcrvals an: equal. the model may be c:.xpn:liICd as:
£(Yp) =/1 + a; +.7rj + Yk
when: /l is the inll:RcpL a, the efl'eet or . . f_ die ilia (/= I •.... I) inlen'aI. lrJ Ibe effc:cl of period far &be jlh U= I ..... J) inlCmll and die eJTect Ihc kth callOd (k=i-j+l= t ..... K=I+J-I). 'lheusual c:onsIIaints in this madel imply dIa. Ea,= E~J= EYA =0. '1111: _ntiaability plUblc:. manircSlS illelfdnugh a single: unidentifiable palBlllCtc:r (Faenbc:rg and Mason. (979). which can be ~ easily sc:cn if we partitioa each tcmparaI efl'eet into compo-
r.
or
30
40
Age(yearB)
__period cahort . . . . , . lsIs diagtam showing the RJItJtionship beIween age, period and oohott. The dagonaIline tnIc8s III/8'11IHiOd lfelime toran intIvkIuIII bam In 1947
.. -
... .... e["gt] =/l + (;!J" +a i) + (jll" +~i) + (lcll" + y.:) =JI +
-iUJ.. +/l,,) + -i(JJ" +/l.,) +a;-
-
.....
+.7ri+1". because Ic = } - I. Th..... caeh of the curvalun:s can be: lDIiquely delalnined. but dae 0\'e11l11 sq,cs 1ft hopelcssly c:ntaqlc:d so that only CCIIain CICIIIIbinatians can be uniquely cllimated (HolfonlI913). '1111: implication or the: identifiability pnJblcm is thallhc: ewerall dim:tion of the c:O'c:cI far any or the ..... 1CmparaI companellts cannaI be cIc:b:nniaecI fium a ~lR'ssion anal),sis. Thus.. we: cannoI evc:a detcnnine whether the tRmds an: inm:asiq ar declasiq with cobad. far instanc:lc. '!'he sc:cond ftgun: on PIIIc I displays snc:nI combilUllians 01' age. period and cohort parameters,c:Kb SCI ofwhich JllDvicIcs' an iclc:nlical Ic:I of filled rates. Nalicc that as Ihc: period
7
AG&RELATEDREFERSNCERANGES ________________________________________________ panuaeIeIS an: IObdc:cI clockwise:. the age and cobalt panImdc:n an: eomparably IQlaIcd in abe counterclockwise dim:tion. Each of these parameters can be IObdc:cI a fuU 181)0. but it is importDDl also to n:alise that they cannol be
IOlIIII:d one at a time.. only all together. n..s. even thOUlh the speaRe tIaIds cannaI be uniquely cstimalcd. certain combinatio.. of the overallln:nd can be uniquely delennincclsuch as!J" +{J". which is callecl Ibc nel drijJ (Clayton and Schil1lcn.. 1987a. 1987b). Alk:maIive drift a.timata covering shaner timcspmas can also be dclcnniDcd and these have pnldical significance in ta.abey describe the experience orfoUowing a palticular age paup in lime, because bath period and cohort will advantIC lOgeIhcr. Curvatura. by way of aJIIlnIsl. are campldcly cldcnnincd. including paI)'DDIDiai panunden for the sq~ and higher powers. changes in slopes and second difrc:n:nc:es.. The signiftcancc test ror anyone of the Ic:nlporaI eft'ccts iD the pracnce of the 0Ibcr two wilileacrally be aacst of abe conaponding curvatun: and naI the slope. Holfonl piovidc:s rudhcrdcrail an how software can beset up for fitting these models (Holford. 20(4). ' TRH aa,toa,D.............. E. 1987a: Models for temporal wriation in caliccr I1IIC5 I: Ap-periocland ~ahort madcls.. SlatUli('s in MftlidM6, 449-67. a..., D...... SchIfIInI, E. 1987b: Madcls for temporal ~ in cancer riles D: ~ ClDhon nladelL St,,'isliaill aVecIi('ille6,469-8J.I1eJIbIq,5.E..........., w. M. 1979: lcIeatilicalion and cstimaliaa or ~period-cobod models in the aaaI)'sis of discmc. .bMIl data. Sociolori('tll'MelhoiolDgy 1971.1-61. Halford, T. R. 1983: Tbc cSlimaliall of age. pcrioII and cohorI drects rar vital rates. BiDlrwtri('s 39. lll-24.1IoIfonI. T. R.
2004: TCIIIpCII'II flldals in public heal... survcillance: SCIItiDg aut age. period and CCIhart dfeds.1D Bsookmc)'CI', R. and Sbaup. D. F. (cds). aVDllilDrinl tbe bealtb 11/ populstitNu. Odani: Oxford Uai\'CISiI)'
PIal. lIP- 99-126.
age-ralatedreference ranges 1besc an: ranges of values or a mcasu~mc:at that identify the upper and Iowc:r limit of nannality in lhe population. w~ the range varies according to Ihc subjecl'S age. Rcfcn:nce l'BIIIes are an important put of medical diapasis. w~ a conliDUDUS mcasU~lI1CIIt (e.1- blood pn:ssun:) needs converting 10 a binary wriable fardccision-making purposes. If the patient's value lies outside Ihc measurement's reference range it is tn:atccI as abnormal and the palicnt is invcstiptc:d further. The canSlJUclion or refcrcacc I1IIIgcs involves estimatinl lhe range or values that CO\lCJ'i a spc:ciftc:d pm:enlqc or Ihc ~ren:ace papulation. often 9S .... Usually this is the ccntnl part of lhe distribution with equal rail an:a probabilities. allhaugh in somccascs the ~ren:nce range is baundccI at zero or infinity. For nonnally distributed cIaIa the range can be fnmI the population ~ and STANDARD DEVL\11O.'f (SD). die 9541, nmgc. for example. being the meaD plus or minus 2 SOs. For nannormal data the simplest approach is 10 use quanliles. i.Co rank and caunt the data. then the 2.5CJ. and '¥IoSCJ, points are Ihc lower and upper limits or Ihc 95 CJ, referaICC I1IIIgCo However. this is indlicicnt and n:quircs a large sample. If the data an: sIcew they can be iransronncd.. e.g. to lopritlumi. and then the refcrcacc range can be calculllled f..... the mean and SD on the transformed scale
cIeri_
2.-----------------------------------------------------------1
0.5
-1
-1.5
~
_
........- ........--........- .........--........--........- .......... .........
--........- ....-..-
.......- .......- ........
..M._......._.M...._.M...._
_ ......._.
........--.....~.~.-.........- .........- .......-.
........_ ........_ .........M_.......
. . M._........._ ........_ ......._ ......._ ......M_........_ ........
M .......
......
PerIod slope
-0.00 -0.05 -0.10 -0.15 -0.20
-I--
~.5~------------------------------------------------------~ age period cohort 1InIIIys. AiJB. pIHiodand cohof1 efIeds torpm-menopausal bnHlsI cancer incidence for SEER 19~1~
,
_________________________________________________________
AG&S~F~RATES
1m~------------------------~
180 -140
f -
12OJ------
I! 100 L-------~ 1m.·············· .. I. ..................................................
1
80 40 .......................................... .
........................
20
o~----~------,-----~------~ 1.. 19 24 Age(J8ars)
.....,..... ....iance . . . . AgtHe/ated 95" reIetence ranges for blood Pf8SSUte In boys: systolic (solid lines} and diIIstoIIc (dolled Hnss} andlnnsfGllllCd back 10 Ihc: original scale. A JIIOIe ftexible variant is 10 use a 8oJt-Cox power tnmsfomudion (of' which the laprithm is a special case). which adjusts for slcewaess more prmscly (sa: 'IIlANSRJIW.VIO). A&e«laIcd refen:nc:e nnps an n:feIaIcc l1IIIIes that dc:pend on DIe. They arise mast commoal)' in paediatrics. notabl), for apHelalccllllCaStRS of'bod)' size like hei&ht and weight. which can be displayed as CIIOW11I awns. The priac:iples or reference IBIIIC eslilDalion ale CSICIIliaU)' the SIIIIIe wilen they an: age re'aIaI. exC:Cpllhat Ihe JDD&CS Cor adjacent BlC JIUUPS aeeclto be consisteat. To awid clilCOlllinuiIic:s at the 8IC lmap boundaries .requires the sUIIUIUIIY slatistics toclefine the refereDCIC nmce (e.I.the mean ancISO) andtocbanpsmaothl)' with lIIe butimpasiq this constraint compIicarcs die fitling piQCess. For normaIl)' distributed homosccdastic data, when: the SO is coastanl ac:nJSS BIC. the lIIe-n:lated mean can be eslimllb:d by LINEAR IWIRESSION and Ihc: Jd'en:nc:c map cxmsllUcted 8IOUIId the regrasiOD cane using the n:sidual SO. 11M: rqrcssiDn curve is estimated asinl a smoaIbiq repalion fUnction. e.1- a pol)'llDlllial. Iiac:IionaI polynomial or lencrarllCd addilhc (cubic spline) cunc.lfthe SDchanps witb . . u is often the case. a c~ of Ihc: ap-related SO also needs to be estimated by the n:p:ssiaa methods or Aitkin (1981) or Allman (1993) and the Ble-reIaIccI me.. obtained usiq wciJhtcd linear relR:Ssian willa weights com:spollding to the imene squan: or the Ble-n:lated SD. 1'bc age-relatccl Jd'en:nc:c mqc is apia COIISII'IICIaI araund the repssioD CIII\'C using abe SD curve. When the cia.. are skew it may be possible toacljUSl for the skewness ..... a single. col. logarithmic. 1ransf0000000on at all asCI. However. often the cIepec or skewness is iiself' age ~ althouP this needs a large sample to show iL .. this case an 1IIe-n:Jated sWlI1IIIII)' slillistic for the has to be estilDlllecl, alGIII with the ....relalal mean and SO. The
_wness
UIS MEIIIDD isa papuI.-way todo~is, or altemmvelythcEN method of Royllon and Wnpa (1998). For IIIIR extn:me
IlDllnormai elata, a nOnpanuneIric appmach based on QUA.N1D.E PElWfSSIlN i5 ncecIecl. a fonn of least absaIUb: enors n:p:ssioD. when: smoaIh curves are cOlllbuc:led for the agerelated upper and IGWa' limits of' the n:feraace ranp. 'I1Ie figure livcs ase-n:JaIcd refelalce raqes for systolic and diastolic bloacl preIIUfC in boys.apd 4-24, estimated by the LMS methacI. ~ an: two advanIaps of'refeninte mnps based on an undedyiq fmauenc)'distributioa. uapposcdto~cIeri_ . . . quantile rcp:ssion. TIle lint is eflic:iency - the standard c:mmI ofb refen:noe I1IIIJC limits are smaller. 1b: SCICDIId is
anaI)'licai conVCIIiencc-daIa for indivicluals can beconvenccl loz-SCORES.. indicating how many SDs they an: above or below the median of the c:IisIribulion. wllic:h is a convenienl way of adjullilll for. prior 10 fUrther analysis. TIC (Sec also 0I0W1II awnsJ
AlIda, M. 1987: Madcllilll Y8riIIxe hc~ in IIGIIDIIIqIasicIa asilll GUM. App/iIIJSlflIlJIlcl36. 332-9. Mala, Do O. 1993: CalSlructiaaafap«laIaIicLaxeccntilcs......... aidulJs.
StlllirlnillM«Iit.W 12. 917-24. Cole, T.J.... Ona, •• J.I992: 5'nIDaIhiac n:fCJCIII!C ccnlilc CIII\'CS: ~ LMS IiIdhoIIIIIII peaaIizcd IibIihDocl. Sltllistin iIr IIft1lrine II, 1~19. KoII*tr, R. W.... D'O"'t V.I987: ~"",,""'.ApJIIWSttIt&lirl 36, 383-93• . . . . . , P..... WrlPt, JL M. 1998: A IiICIhod far cstimd.lIMPCCific Id'CftIICe illlCnlls ('nonDaI raps') based an
fraI:tiaaaI paIynamiIk and apanealiallIIIIsfarmIIIia JourtIIIIof" un. 79-101.
IlDJYII SIIIIiMiaII SDci6y sma A,
.......,aeHIc rates
These an: rates calculated within a Dumber of Kialively Dl1IIOW' ap bands. A ClUcIe rate is the: Dumber or ewmls occurriq in a papulation duriDg a speciftecllime period divided by an eSlilllllac of' Ihc: size of the:
I
AGRESMENT ________________________________________________________________
populatiOD. However. when comparinl rates belween populations willa diffen:nt !lie dislributions. it is necessary to consider IDles at specific ages separately. In the table:.. clealh rales an: pn:sc:naed for COIla Rica and Ibe UDib:d Kinplana for 1999. derived fna dala flUID the United Nations (2002). The final colunm lives the SICspecific rales far bmad !lie bands and the crude (lotal) rate. The QC-specific rate is calculated as the number ofdeaths in Ibe palticular DIe lroup.ln Costa Rica. thc death rate aI ages 0-5 is calculated as 129611 070000. 'I1Ie rate isexpmlSCd per 1000 penons so the nile is multiplied by 1000 to live the rate of 1.2 pel' 1000 in the final column of the table. .....pecHic rates Population, number of deaths and deaIh I8Ies from all causes lor Costa RIca and tire United Kingdom for the YfHU 1999 CD~III
RiclI
A,e
PtlplllllliDIr
'96 in.II,e
11'0"11
(IOOOOD.s)
gl'tlllp
0-15 15-49
10.7 17.4 3.9 1.3 33.4
32'1\
50-69 70+ Tala)
12 '1\ 4.,
DmIJu
DeIIIIr Nle//ODD
1296 2766 3447 7523 15032
1.2 1.6
8.8 56.6 4.'
Uniled Kirrgtlom PtlpIIlllliorr
'96 in lI,e
(IOOOOD.s)
gRlllp
0-15 15-49 50-69 70+
113.9 288.0 126.1 67.0
TaIaI
59'~0
DmIJu
DeIIIIr Nle//ODD
19 'I.
S8SO
48~
31228 120759 474225 632062
0.' 1.1 9.6 70.1 10.6
21 '1\ 11'1\
RATIOI 0.... far N...... staIIItIcI 2002: MorlDli" "D'islier mII.ff'. R~,~,,· oflM bgalr. G~I'tIIIIII_11u ilyeDuse, .x_IIg~. in
ErtglDRJ _ WDks. 200/. I.oadoa: Ofticc for NIIIioDaI Statistics• PmtdD, M., WIIeIaII, So, FIrIa)", J., TIppO, L -1'IIaIaaI, D. B. 2003: Olmw iItritImt:r iIr ftl'e ftHIliIIt"ls. ~l. VOl. Lyan: IARC Scientific Publicldioas. Valid Na_ 2002: 2000 tltmogrtlphic )WlrbooIc. New VOlt: UnilCd NIIIions. WaI... A., ........ J., CaaBard, .... GaddanI, Eo ... M. 2001: liI'ing in BrilDiR: re.ll~from lilt 200D c;,lItrtll HoaseIroIti SlInyY. Landan: 11Ie Stationery Offtce..
n-.
52~
Age ,,.D"II
00la: of NaIi..aI Statistics (ONS) in Ensland and Wales (ONS. 2002). Ase-spc:cific disease incideace rates are also published in wrious cauntries, mosI DOIably cllllCer incidence. for which inlclnalional data an: compiled by Ihe Inlemalionai Asency for Research OD Canter (Parkin el QI•• 2(03). Age-spccilic prevalence ndes for exposures such as smokinl can also be derived. but ~ mon: usually obtained from specific surveys such as Ihe Oenn Hause:hold Survey (Walker etlll•• 2(01). HI (See also CAUSE-SPEC'mC DEA1H RA1E.. STANDARDISED . . . .AIJJ'Y
The: crude: (talal) rate forCosta Rica is less than halflhat for Ibe UK. However. at DO age is the nile in the UK double that for Costa Rica and far some qe groups the rate is higher in Costa Rica than in the UK. Note that the pe~nlQc:s of the populalion in each age group (third column) diller markedly. The UK papulati.. is much older (II .., of thc population ~ oyer 70 compan:d with 4'1\ in Costa Rica). The different . . st~ explaias the misleadins mmparison between the crude rateL Agc-spec:iftc rates are cwnbenomc: to mml'lR across a number of populalions. Standardisation mc:lhacIs are often used to provide an qe-adjusted sunurtal)' nile far each population.
Many countries publish qe-specific ntc:s for all cause and specific causes of death. c.l. tile annual publications of the
8gl'88lllani Apeement in repeated assessments is a funclameatal crilcrion for quality of usessmenlS on mtins scales. The use or ratinl seales and ather kinds of anIercd cllllSi6calions of complex qualitative variables is inlel'disciplinuy and unlimilc:cl. RatiRl scale assessments produce tlrr/ina/ the anIemI caleCOrics JqHaentinl only a rank onIc:r of thc intensily of a particular variable and IIDI a numerical value in a IDIIthemalicai sense. althqh the use of numerical labelliag could give a false impression of quantilalive data. (sec RANK INVARWICE). The main qualilY concepts of scale assessments are reliabilily and "alidiIY. Reliability (sec ME.o\SUItEMENT PIECISION AND REl.lABlury) refers 10 the extenlto which repelllecl measun:ments of dae same: abject yield thc same raula. which means IIIR'Cment in n:peated usessments of various designs. In intell1lk:r n:liabilily (see MEASUJlfJ.I!NI' PRECISION AND REUAllurY) studies an: madeofthc level oragn:emenl belween obscm:rs duat classify the SIIIIIC object or individual. and inlnlraler reliabilily (see INrRACUSS CORREl.ATION COEFFICIENT) slUdies refer to ap:cment in lesl-relesl scale usc:ssmc:nts by dae
.'11.
same: nIIcr. the f""lucDC')' disbibution of pain of ordinal data is described in a square COJrnHOEI'D' TABLE (sec the figure wilh pans I, II and III on page II). and in the cue of continuous usessmenls on a visual analogue scale. VAS. by a scllllcr plot. 'I1Ie percentage apecment (PA) is a basic agn:emc:at meas~. When theqreemena is unsatisfactar)' small RUDDS f.disqn:ement ca bce'Vllluatc:cl by a &IaIisticai meIhod lhal labs Kalant of the rank-invariant propc:dic:s or antinal clata and thai makes it possiblc 10 identify and measure systelDlllic disasn:ement. when 1B1CDt. separately from disagn:ement
________________________________________________________________ AGREEMENT
Systematic diSllJl'CCmcDl is evident by the lIIBIIinai helUogencity. and by pairilll otT abc two sets or lIIBIIinai rrequencies. the so-called nnIt-lnInsrannabie pattem of &p:ClDent (RTPA) is cODstnlclcd. The RTPA clc:scribcs the expected paltera in abc case of systematic disqn:emc:nt only. All pain or observations or the RTPA will have tile same rank onicrilll in lhe two assessments provided dial the ranks am lied to the cells. which is the clcfinilion or the augmcnled ranking pnJCCdun: (aug-nmb)
caused by individual variability in assessments. SySlemalic disa&Rcment is population based and maIs a sySlemalic duuage in conditions or memory bias bcIwccn 1CSl-n:1CSt assc:ssmenlS. or bclWccn ndcI5 who interpn:t the seale caIelDries ditTeratly.l..arJe individual wriabilily. on the aIhcr haad. is a sip orpoorqualily ora ralilll scale as it allows for uaccrlainty in ~1Ilcd assessmc:atl. TIle pracnc:e or systematic disagn:c:mcnt in Ihe use of the scale calCpric:s between the two usc:ssmcnts is ~ed by ditTcrcat fRe quency dislribulions. which means IlUll'linal distributions (paris I and II). A systematic disagr1:clDenl n:pnIiac the categorical levels and in the way or concc:allatin& the asseamenlS on Ihe categories ~ mellllUml by the n:lali~ position (RP) ..... the n:lali~ conccnlralion (RC) n:spcctively. The RP expn:sscs the extent to which the IIIBIJinal distribution of assessments Y is shined lOWanIs hillier categories than the lIIIIIIinai distribution or X. nather ..... the opposite. A lheon:ticaJ clcscripti_ is the: diR'c:n:nc:e bclwecn the probabiUtics P(X < JI) - pcY < Xl. Possible values or RP ranie from (-1) 10 1. and RP is positive whcll higher seale calcJories ~ more frequently used in the assessments Y than in X when CXIIIIp8I'Cd with the opposite. Com:spondingly. Ihe RC expn:sscs Ihe extent to whieh the IIIBIJinai distribution or Y asscssmen15 is II'ICR COIICCnlndcd to central seale catcgoric:s than is the rnaqinal distribution or X. thc:oIclicaily clcscribecl by Ihe diR'c:n:acc in probabilities P(X,< r,,<x,)-P(Y,<X,, < lj). Possible values mnge from (-1) to 1. and a posilive RC indicates thai Ihe assessmcnlS r an: man: CXIIICCntratcd than x. Zao or wry small values or both RP and RC mean lhat the systematic part of an observed clisqrccmenl .-ireel assessmeats is ncglipblc.
I A
RaIcr
r
RatcrX B C
D
I
I
D
c
II tat 2
A
(sec IAXKINO). Part U in the figun: is the RTPA orthe pallem in part I. The observed distribution or pairs in part J deviates from this
RTPA. which means that some or the pain or aug-ranks given to Ihe observations diO'er. The relalive rank yariance (RY) is a rank-based IDCDSUK or this observed individual variability. i.e. unexplained by the measures or SyslCmalie diS81n:cmcnl:
when: n is the number or paiRd assessments and (.di,)1 is Ihe squsn: or the mean 8U&-lDllk diR'en:ac:e of the Qlh cell. ad the summation is made over all cells ij or the m x n, square table, 0 ~ RV ~ I (Swnsson Itl DI., 1996; Svensson, 1998&). TIle Cohen's coelltcienl kappa (,,) is a commonly used mcasun: or 8IrecmeDt adjuslccl ror lIIe chance expected qn:c:mc:nl (sec KAIIPA AND WEIOII1'ED KAPM). the calculations of Cronbach's alra and other so-called n:liability CXlCl1icicn15 an: baed on the lIlISumplion or quantitative, normally clisbibutcd daIa. whieh is not achievable in
RalcrX B C D
tat
'Z
Z
IJ
2
'·Z.
14 18 C
t 16"
B
1
1
II
3
16 B
A
2
8
3
1
J4 A
tal
3
II
17
19
PA.12'1 RP. -0.49
RV,o.OB
17'
3 11
!50 tal 3
II
17
19
RP,-G.49 RV.O
A D
RatcrX B C
D
I
4
14
tat .9
II C
1
2
10 4
17
16 B
1
6
3
II
14 A
1
2
50
3
II
tal
1
3 17
19
!50
PA,62~
PA.12" RC.O.l6
OJ
R~0.16
RP=RC.O
RV,o.OS
agraement EJtIJmpIes of psifed ordinal data from Intemtter assessments on 8 four-poinl SCIIle with the ORIered calegodesl8belledA < B< C < D. 7beranlc-transfotmablepaltem oIlJ111'f18f11f11(RTPA) Is sIuIded. Themeasul8SoI percsnlllge agreement (PA), lhelflllltive position (RP), Iherel8t1ve concenItaIion (RC) 8IId the 18Ia1lve mnIc VBIfance (RV) 818 given
11
AKAIKFS INFORMATION CRITERION _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ __
data rrom nding scales. There is also a widespread misuse or the correlation coefficient as a reliability measure. The eorrclalion coemcienl (see CORRELATION) mcasun:s the degree of associalion between two variables and does nOi measure the level of agn:ement. In part I of the figure the PA is 12~. and the observed disagreemeat is mainly explained by a systematic disagreement in position. The negative RP value (-0.49) and the RTPA (parlll) shows that the assessmenls r systematically used lower catqories than X. A slight additional individual variability. RV =0.08 is observed. SPEARMAN'S RANK CORRELAll0N COEfFICIENT. r~. is 0.66 in part I or the figure and 0.97 in part II. ignoring the ract that the assessments an: systematically biased and unreliable. The same holds for the eoemcienl kappa (-0.14). In pari III the marginal homogeneity and the zero RP and RC values confirm that the disagreement (39~) is entirely explained by slight individual dispersion (RV =0.05) from the RTPA. which is the main diagonal in this case. The ra is 0.61 and the It is O.4S. Besides reliability studies. the level of disagreement is or main inteRst in paired asscssmenls ·berore and after' lrealmeat for analysi~ change in outcome or treatment effect. In this application or the disagn:ement measures, nonzero RP and RC values indicate the level or eommon group change in outeomes. and the hcterogcaeity in changes among the individuals is measun:d by the RV (Svensson. 1998b). ES Swauoa, E.. 1998&: AppIicatiCIII of a llIIIk-invariant medaod to C\'IIIuale n:liability of ontcmI catepD:al asscs:smcnlS.. Jorulftll of Epidemiology I11III Bioslalillirs 3. 403-9. SYIIISIOII, It. I998b: OrdiDDl invariant measures for indiridual and group cbanp:s in ordmd categorical data. SlaliNlits in Meditbre 17, 2923-36S........, ...... sr.m.tc, J ..E., BboIm, S.. YOB . . . . . c. aad Me....... A. 1996: Analysis of'inter-Clbsen'Udisagrmnc:n1 in die asscssment of subarachnoid blood . . acute hydrocephalus on cr scans. Nftlrological Remuth 18. 487-94.
AIcaIke'slnformaUon criterion
Akaike's infonnalion criterion (AIC) is an index used to discriminale between compcti~ models. It is widely used when then: is the issue or model choice where we wish to find the most parsimaaious model (see Akaikc. 1974). Often there may be a number or possible models that can be Hlted 10 the cIaIa. from which parameters can be estimated using. rorexample. the MAXIMUM UKaJIIDOD ESllMATION. Generally. complex models an: mo~ ftexible. but contain a n:lalively large number of paramclers. whereas simpler models with rewer parameters may compromise the fit or the model to the data. Eueatially. the AIC statistic compan:s competing models by CXJllsideri~ the trade-off between the complexity of Ihe model and the carrcspanding fit of the model to the clata. The AlC stalistic is widely used. particularly as it can be used to compare a'en
models when likelihood ratio tc:sts cannoI be applied. Let z denote the data and' the com:spondi~ maximum likelihood estimates (MLEs) or the pararnclcl'5. Then. the AIC for a given model is denoted by:
IKJIU1CSled
AlC = -2 log L(i; x) + 2p where p denotes the number of parameters in the given model being filled to the data and log L(i; z) the corresponding log-likelihood evaluated at the MLEs of the parameters. The AIC statistic is calculated ror each possible model being considcrc:d. The model deemed optimal is the one with the smallest AIC value. i.e. a model with a relatively small number or panunelers that adequately fits tbe data. The AIC is generally easy to calculate given the maximum or the likelihood function and is vcr)' versatile. allOWing us to compa~. for example. nonnesleci models. We note that c:orrec:tions have been suggestc:d to the AIC statislic to allow for data with ovenlispersion (denoted by QAIC) and small sample sizes (AIC,.). See. for example. Burnham and Anderson (2002), Sections 2.4-5. 1be AIC statistic has also been used to eompare Ihe performance of difl"cmlt models. relative to each othu (Buckland. Burnham and Augustin, 1997: Burnham and Anderson. 2002. Section 2.6). It is not the absolute values of the Ale statistics thal are important but their relative values, in parliculartheir difference. Foreach model the tcnn .dAIC = AIC - min AlC is calculated. where min AlC is the value of the AlC slalistic ror the model deemed optimal. Clearly. AAIC = 0 ror the model deemed optimal: the largCl" the value or .dAiC the poorer the model. The relati\'e penalised likelihood weights n', can also be calculated ror each model i = 1•. , '. m. where: W; =
exp( -.dAlC;/2)
-=",r~----';':"""";'-
Eexp(-AAlCj/2} j=1
and AICI denotes the carrcsponding AlC value associated with model i. The weights provide a scale to interpn:t Ihe difference in values ror the models. Finally. these model weights can be used to obtain a (weighted) model-averaged estimate or parameters of interesL RK [See also DEVIANCE. UKflJIIOOD RATIo) Ablb, H. 1974: A DCW look atlhc Slatistical model identification. IEEE TrtmJGt:lioRs on Alliomalit COIItrol AC 19. 716-72, Backlaad. S. T., BIIlIIIuua. K. P. ad Aapstta, N. H. 1997: Modcl selection: an integral part of inrc~nce. Biomelrirs 53. 603-11. Bu........... K. P. &ad Andenoa, D. R. 2002: Model sc/~clion aM mullimotlel i"J~rDlte. 2nd editiCIII. Heidelbell: Springer Verlag.
_ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ ALL SUBSETS REGRESSION
allelic association
1'bis is an association between two alleles (at two dilTermtlaci). ar betwcea an allele and a phenotypic bait. in Ihc population. Since humans IR diploid a morelc:dmical definition of the ranner is nca:ssary: two alleles are associated iflhcir frequency orCO-OCCUJ'RDC."C in the same: haplolype (i.e. Ihe genetic maIeriaI transmitted from one pan:nt) is gmder Ihan the product of the l1III'Iinal frequencies of the lwo alleles. Association belween two alleles is also known as lilrJcoge dlseqrtili"'iuIII. 1bc reason is thai. in a lillie papulation under mncIom mating.1hc extent of association between two alleles (as me&lllRd by the difference between Ihc rraaucncy of the haplotype containinr: Ihc two alleles and the product or the frequencies of'the two alleles) clc:c:reases by a radar equal to one minus the n:combinalion fraction (see OENETIC UNIt. AGE) between the two loci. per leneration. "Ibus allelic association n:pn:sents a slate of disequilibrium that k:ads to dissipate at a nile determined by the sln:nlth or linkage the stale of equilibrimn belwcen the lwo alleles. whea the: frequency oflhe haplotype is equal to the produc:cor the hqucncies of the two constituenl alleles. AssociDlions between lWO alleles can arise in a population for a number of R:8SDRs. The mutation that pve rise to the more rc:ccnt allele may ha'Ve occuned on a chromosome tlud happened to contain the other allele. Random genetic drift duriq a population botdeneck may have led to the oVcm:pR:SCntalion or some haplotypes. The mixiq of two populations with differenl allele frequencies may havc resulted in associations between alleles in the ovmall population. When. for any of' these ~asons. such allelic associations arose many lenemtions BlO. OIIly those occurring between lightly linked loci are likely to havc penisted 10 the Clll'l'CDt ICDeraliaa. We would thcrefce expect an impelf'ed inverse rdationship belween Ihc extent of associalion between two alleles and the distance belwecn 1hc1D. An assocwion between an allele and a disease may be lhe result Oradi~cl causal Rlationship.ln other words. the allele is a causal varianllhal is fuactional and increases Ihc risk of the disease. However. il could also be indin:cl. with the allele beiDg in linkage disequilibrium with a causal variant. The pI1:lICIICe of' link. disequilibrium belween tightly linked loci means that it is possible to seRen a chromosomal n:gion for a causal varianl without eumininJ all the alleles. only a sufticienl number to ensure Ihat any causal variant in the ~gion is likely 10 be in linkage disequililximn with one or mon: of tile alleles examined. The poIymorphisms chasen 10 JqJn:5Cnl itself and associated polymorphisms in ils vicinily in an association study are called TAG polymorphi&ms. The International HapMap Projecl (www.hapmap.DII) has characterised the pauem of allelic associations among over 3 million sinlle nucleolide poJymorphisms (SNPs) in the human lenome in line major populDlions (Europeans. Arricans and Asians).
lOW'"
.Classical epidemioloJical designs (CASE-coNI'IDL SnJDl!S. COHORI' STUDIES. CROSS-5EC11ClNA1. SnJDlES) are mldily applicable to lhe study or diseasc>oallele associations. as IR the Slatistieal methods developed ror Ihcse designs (e.l. LOOIS11C REORESSION. SURVIVAL ANALym). These designs are polCDliaily susceptible to Ihe problem ofhidclen population stratiftcation. which can lead 10 spurious associations or mask true a~ cialions. Family-based association designs an: robuSl to population stnliftcaliaa and usually consist of the use of eilller parenlal ar sibling controls. Melhads forlhe analysis of matched samples. such as the McNBIAR·S 11!ST (also called the transmission disequilibrium lesl in the contexl of'pamatal conlmls) and CONDITIONAL LOOJS11C RBJUSSIDN an: applicable 10 these dc:sips. The study of diseasD-8llele associations is a complemcnIaIy slndegy 10 link. analysis. in the localisation and identification or genes thDl incn:ase the risk or disease. In general. allelic association is unlikely to be detected when Ihc marker locus is quite far (>1 mclabase) from the disease locus. but can be much mon: powelf'ul than linkage whea Ihe marker locus is close enouP to the disease locus to be in substantial IiDkqe disequililxium with it. particularly when the effecl size of the disease locus is small. For this reason. allelic assaciation is particularly appealiq for sc:archillJ n:gions that demonstrate linkage to Ihc disease or to Ihe inveSlilation of specific candidate aenes. However. technoIopcal developments have enabled lhe efficient lenolypiq of up 10 I million SNPs in a single 8II'8y. and this has led to association sludies on the whole-genome scale (called gellOl11C-widc assoc:iation studies. or GWAS) that ha'Ve coverage of over 90 fJt of common variants (allele frequency > S CJ.) in the lenome. PS
all ..bsets regresSion
A form of n:grasion in which ull possible models an: compared usillJ some appropriale criterion for indicatinllhe "best' models. If there an: p explanatory variables in the data. there are a total of I
r-
possible reIRssioD models because each explanatory variable can be in oroul ofthe madel and the model containiq no explanatory variables is excluded. One possible criterion rar comparinl models is the MAu..aNs C,. STA11STIC' and 10 iIIur lI1Ile ils use we will apply it to data that arise from a study of 2S patients with cystic ftbrosis Rported in O'Neill el til. (1983). and also gi\'en in Altman (1991). Data for Ihc first tine patienls an: Jiven in the lint table. The dependenl variable in this case is a mcasu~ or malnutrition (PE_). Some of Ihe models consideml in the all subsets n:gression of Ihcse data are shown in the second lable. Iogcther with their assaciated C,. wlues. where p n:fers to the number of paramelcls in a particular model. Le. a model that includes a subsca of p - I of the explanalaly variables plus an intercepl. If Cp is plouecl against p. Ihc subsets of explanaIDry
13
ALTERNA~HYPOTH8S~
_______________________________________________________
all .uba. regression Cystic flJrosis data; fbI thl8fJ subjecIs Sub I 2 3
7 7 8
Se.T.
Height
Weight
BMP
FIN
RV
o
109
13.1
1
112 124
68 6S
32
12.9 14.1
19
6S
22
o
FRC
TLC
2S1
113
24S
137 134
95
449
441
268
147
100
85
Sub: subjcc:t number Sex: O=maIe. 1=female BMP: bady mass (ftiJhIillc~) as • pcrcen1age or Ihc agwpcc:ill: median in IICInII8l indiriduals FEY: fon:ed cxpiratary volume in CIIIC secand RV: raiduaJ wIume FRC: filDclional residual capacity TLC: lotaIlunc capacity Pf..u: maximal statistic clpinllOl)' pn:SS1R (cmH:O)
alternative hypothesis all ....... regie_on Some of ths models fitted in ~ths~ _ _~~m~~~.~
data (size is one mote than ths numberofvllliables in. model, 1o Include the Intercept) Model 7 14 21 ~
3S
42
2 3 4 4 5
63
6 6 7 I
70
9
77
9
49 56-
Tnnu
Size
Sex Sex, weight Age. FEV. RV
Age. BMP. FEV Sex, weight, BMP. FEV Ale. wei&ht. BMP. FEV, RV Age, sex. height. FEV. TLC Age. sex. height. FEV. RV, n..c Sex, weight. BM.,. FEV~ RV. FRC. TLC Age, height. weight. BMP. FEV. RV.FRC, TLC Ale, sex. height. BMP. FEV. RV.FRC,TLC
Cp
17.24 4.63 2.62 4.5 2.95 2.8 6.99 7.06 6.49 8.06
10.29
• Models close to abc line e,. =p. variables mast wonh cODsidcrini in trying to ftnd a parsimonious model am Ihase Iyilll close 10 the line C,,=p. All subsets IqIasion has been foUDd to be particularly userul in applicaliOM or 'COX"s REGIlBSION MODEL (sec Kuk. 1914). SSE (See also MUL11FLE LINEAR RBJRESSION] AltmaD , D. O. 1991: PrortimJ stillwiea for rrwdiml remut:b. London: CRCJChapman & Hall. Kale, A. Y. c. 1984: All subsets ~ion in a pruportioDaI hazuds model. BioIrwtrim. 71~.587-92. O'NtIU. s., ....." r., PasCerIcaInp, H. aad Tal, A. 1983: The dfects of chronic bypmunclion. nutriliaaaJ staha and postuK on rapiratar)' muscle sbmIIh in cystic fibrosis. AlfWriftlll Rft'ieM' of Respiratory DiJortlers 128. 1051-4.
AMOS
See IIYIVl1IESIS nsrs
See STRurnJRAL EQUATION MDOEWND sm:rwARE
a..lysls of covariance (ANCOYA, ANOCOVA) This is an extensiao of the analysis or variance (ANOVA) that incorporales a eantinuous cxplanalOry YDriable. When: ANOVA aims to ddc:ct if then: is a change in the mean value or a wriable across two ar IIICR puups, ANCOVA (or rarely ANOCOVA) docs the same but adjusts for a mntinuous covariate. Most commonly this cowrialc will be a baseline ~~ menl, a1lowinl the analysis 10 adjust ror initial variation between participants and isolate the etrects due to the lRatment factor. However. sometimes a dift'en:nt covariate is used. Far example. Xarhune el QI. (1994) consider the association' bc:twccn alcohol intake (divided into rour cllle-garies) and numbers of Purtinje cells. In doing so they introduce DIe as a continuous covariate in order to 'control' or 'adjust' for the effects of age on cell numbers. Under other cirannstanc:es the aulhan 'could have been inten:stcd in the etrects of age and wantinl to adjust far alcohol intake. Despite being the same analysis computationally. this is not typically what is lhought or as analysis of covariance and might mo~ commonly be IR5Cnled as a '~grasion' . Indeed the various analysis of wriance methods can all be Yiewed from within a repession fnIInewoItt. which demonstrates that ANCOVA can be extended to cope with much m~ than ODe continuous mvariate. Malhematically. ANCOVA follows a similar path to thal far ANOVA and the output is usually summarised in a similar table. aJlhoUlh the details may vary. The promised beneftls of the analysis of eovariance an: clear. If one has an unbalanced obserwtional study. then ANCOVA can adjust for dift"en:nces in baseline 'Values and ~movc a potential bias from the ~sults. By the same token, if one has a randomiscd biaI thai is naturally balanced. then
_ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ ANALYSISOFVARIANCE (ANOVA)
ANCOVA mluces the amount of unexplained variation in the data and Ibus increases the power of the test. However. ANCOVA can only be employed if the appropriate assumptions are met. 'lbcse include those of ANOVA (i.e. normality of n:siduals. holllOSC."Cciaslicity) as well as the appropriateness of the ANCOVA model. Is the n:lationship with the covariate IrUly linear? Docs the etTc:ct of the COWl'iate vary between groups? Failing to meet these assumptions can lead to the introduction of important but subtle biases. It is a frequent c:onccm that medical n:scarch papers report a covariate as having been "conlrOlled' or 'adjusacd' for, with no evidence that the conlrOl 01' adjuslment was appropriate. For further- details sec Allman (1991), Owen and Froman ( 1998). Miller and Chapman (2001) and Vickers and Allman (2001). AGL (See also GIlNER.wSED LINEAR Mooa.l
AItawI. D.O. 1991: Pmt:tiCill statistic's lor mttliml researm. London: ChIpman &: Hall. KariIuDe, P. J., ErldDJutti, T. &ad LalJIPaIat P. 1994: Moderate alcohol ccaumplion aod loa of' cmbcllar Prikinjc cells. British M«Iim/ Joumal 301. 1663-7. MOler, O. A. and CIIa......,J. P. 2001: Misunderstanding anal)'lls of covariaDc:e. Journal ofAbnormtJI PS)~lIoIogy 110.~. OweD, S. V. aDd Ji'I'oawa, R. D. 1998: Uses and abuses oflhc analysis or CO\'lIriancc. Rt.seorm in NlII'sing and Hm/11r 21, 557-62. Vkken, A. J. aDd Altman. D. O. 2001: AnaI)'s~ coatrolled trials with basdiae and follcM'-up measun:mcnts. Britislr Medical JDllT1ItIl323. 123-4.
analysis of variance (ANOVA) Often referring to the one-way analysis of "'ariancc. it is a test for a common !.lEAN in multiple groups that we describe in detail here. Analysis of variance frequently arises in the comparison of more c:omplicaled models, but the same logical argwnenlS apply. In all eases. the undcrIyiRl concept is to partition the observed wriance into quanlities attributable to specific explanatory soun:cs. and then consider important those SOUK'es thai explain 'more than their rair share' of the variance. Despite the confusion sometimes caused by the name. the one-way analysis of wriance is a method for testing to sec whether multiple samples come from populations that share the same mean.. In this mspcct it can be viewed as an exlcnsion to the '-test, which assesses whether samples rrom two populations share a common mean. An analysis of variance performed on two samples is equivalent to performing a l-lest. ANOVA assumes that all the samples come from populations with a NORMAL DI5TRIBU11O.~ that share the same VARIANCE. It can be viewed in a number of ways. but essentially allDpare5 the estimate of the variance obtained within samples (that makes no assumption that the populations have a common mean) with an estimate of the variance rrom the sample means (which will requin: the assumption that
the populations have the same mean). If the two estimalCs of the variance an: different. then Ibis is evidence Ibat our assumption of equality failed and. therefore.lbat the populations do not all have the same mean. Note that the variance of a single sample is eslimated as Ihe sum of squared ditTen:nces from the mean divided by the sample size minus one. 1be sum of squared differences tenD is interpretable as a measure of the total variation in the sample. In the analysis of variance. by combining all groups together. one can calculate this measure for all the data. This is termed the 'total sum of squares' or 'total SS·. Variation in the data is either- "between' or 'within' the samples. The "wilhin poups sum of squares' or 'within sse can be calculatc:d as the sum of squared difren:nces rrom the individual sample means (mther Ihan the ditTen:aces from the overall mean Ihat produced the tcMal SS). 'Between groups sum of squares' or "between SS' can be calculatc:d directly. but is most easily calculated by subtraction of the within SS (rom the total SS. 11ae two estimates of the variance (or "mean square' as it is often termed in this context) can then be calculated. 1bc: between groups mean square is equal to the between SS di\'ided by the number of groups minus one. 11ae within groups mean square is equal to the wilhin SS divided by the number of observations minus the number of groups. An F-slatistic is then calculated as the betwe:en groups variance divided by the within groups variance. Under the assumptions of normality and homoscedasticity (common vananee) Ibis statistic will be an obsen'ation from an F-DISTRIB~ ir Ibe groups come from populations with a common mean. The DEOREES OF FREEDOM of the F -distribution are the number of groups minus one and the number of observations minus the number of groups. From the F-disbibulion. we: can calculate: the probability of observiRl such an extreme value of the F-statistic if the populations have a common mean. This is a one-tailed test. If the value is unusually small. this suggests the between groups variance is unusually small and so is not evidence of variation between the groups. Therefore. the test is to find the probability. ir the populations do have a common mean, or observing a value greater than that observed. A natural way ofpn:scnting ANOVA is the ANOVA table. Given Nobsc:rvalions that fall into k groups. it is necessary to calculate the total SS and the within SS as described earlier and then the analysis can be completed as presented in the first table. Murphy el aI. (1994) conducted an analysis of variance to see if milk consumption before the age or 25 affects bone density of the hip in later life. A total of 248 women palticipalc:d in this part of their study (N =248) and wen: divided intogroupslbat reprcscntlow. mediwn and high milk consumptions (k =3). The samples had similar variances aDd so atlcast one of the assumptions for ANOVA was
15
ANALYSIS OF VARIANCE (ANOVA) _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ __
analysis of variance (ANOVA) 7he anaJys;s of valiance table Degree:lof
SIIIfI:I of
freedo",
:lqutlnS
8etwa:a graups
It-I
Within groups
N-k N-I
Between SS= Total SS - Within SS Within SS Total SS
Soune of l'Qrilllrce
TaIaI
Mf!tJR aqlltlTe:l
F
P
Between MS = Between SS/(It - I)
BetweenMS WilhinMS
p
Within MS = Within SSI(N - It)
analysis of variance (ANOVA) Approximate reconstruction of the analysis of variance table from MulPhyet a/.
(1994). Source of var;lIIIce
8etwa:a graups Within groups
Talal
Degree:l offreedom
Sunu of :lquares
2 245 247
0.15
4A
0.01 0.02
F
p
3.8
0.23
4.6
(Entries in bold weft: infemd from the paper. lite rat simply follow from the cU:ulalioas)
salisftai. As is common for reasons of space. the ANOVA table was not preseated in the published paper. just the Pvalue. but enough dala wm: pn:scnted for an approximate R:Consb'UctiOll. We can infel' btllle within SS is approximately 4.4 and the between SS is approximately O.IS. leads 10 an Fstatistic or approximately 4. From the rcpaned P-value (0.023). it can be calculated from the F-distribution (with 2 and 245 respcclively for numerator and denominator degrees of fR:Cdom) thai the F-statistic was 3.1. The aJOclusion then is thatthc:n: is evidence Ihal these samples cIonot come from papulations thai share a common mean. n.c rcconsb'Uctcd table is presealed in the second table (entries in bold iD this table were infem:d from the papeI'. the rest simply follow from the calculations). It is preferable to conduct an analysis of varillDlX: rather than 10 conducl/-tesls betwc:c:n all pairs of groups. ANOVA awills problems of multiple testing and Ihus keeps CX1IIlIUI oflhe SIDNlflCANCE LEVIiL Having amduclc:d an ANOVA and rejected Ihc hypothesis of common means. it may then be clcsin:d to lest to see which graups ~ raponsible (although a plot of the data might be as infonnalivc). In this case, care must be takea to comd for the problems of making 1ftILDPLE
nus
~.
It is imporlanttotakc: note or the assumptions being made. rather than simply ignoring them. ANOVA can be quite robust to variatio. from nonnality. but hcterosccdasticity can be a serious problem. Residual plots can be used to help assess the normality and IOXPLOIS can be used to help assess the hctcmsc:edaslicity. Passible formallcsts for the assumptions ~ the KOLMOOOItO\L-SMIRNOY 1BI' and I..EVENES 1BI' rcspeclivcly.
If the assumptions do not hold. thea "I1W5RItMA'I1DN of abe daIa mighl comx:t dU. Otherwise a number of nan)Jlll'1llDClric altemativc:s to ANOVA exist. the most commonly used beins the KlUsKAL-W~ 1BI' and the FREDMAN 1I5SJ'. 1bc one-way analysis of variance is appropriate when our data an: simply divided into a number of groups. 'Ibm: an: many other forms of analysiS of ,·arianc:c. 'nIe TW~WAY ANALYSIS CE VARIANCE should be used when the IJOIIPS are definc:d by two factors. S~ for example. we had six groups: the three groups of women in Murphy el QI. (1994) and tlee gruups of men at die same levels of milk atnsumplion. Rathel' than a on~way analysis of variance. a two-way analysis oharianee with gender and milk consumption as Ihe two factors would be appropriate in this instance. Ir the data are multiple observations from the same subjects, perhaps measurements· of cholesterol levels O. 7, 14.21 and 21 days after slarting a new diet 011 several individuals. then a REFEATED ).IEASURES ANALYSIS CE VARIANCE would be appropriate. This is a special case of the two-way ANOVA and can be viewed as an extension of the paired sample I-tell. If lhere ~ observations of ~ than one characteristic from the individuals in several poops. i.e. measures of bulb the diastolic and systolil: blood prasun:. then a multivariate analysis of variance (MANOVA) can be used. If. however. it is desired to correct for a measw-ed baseline atwriate. such as body mass index. in the analysis. then aD ANALYSIS OF COYARIANa. (ANt'OVA) may be used. All these techniques could be implemented through a regRssion framework. in most cases MUIlIPLE lINEAR REORESSION. TheadvanlqeS ofdoing so would be the transition from the usc of a IIYIIOI'HESIS TEST to an actual estimate of etrcct
_ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ ARTIFICIAL INTEWGENCE (AI)
sizes. This approach would also allow IIICR ftcxibility; for inslanc:e in Ihc case ofMurpily el 01. ( 1994) we could account for lhe naluml ordering oflhe 1c~ls of milk consumption that ANOVA ignores. As a gencnl priDc:iple. eSlimDlian and modelling IR usually pn:fenm to testing of h)'potheses. For fUJthcr details sec Allman (1991) and Altman and Bland (1996). AGL
.AJtmu. D. G. 1991: ProdimJ Jla,istk, foT medical l'esearcl,. London: Chapman a Hall. AIIDwI. 0. G. aad BIaDd, J. M. 1996: Slalistic:s nota: oompariag several poups usia: analysis of variaJtI::e. British MedkolJoumol312. 1472-3. M1II'pIJy. s., Ka.w, K.-T.. Ma1. H. aDd Compsloa. J.IL 1994: Milk CIODS1UIIpIion and bone mineral densil)' in middle ~ and elderty WOIDeD. BrilM Met/iral JOIITtIa/ 308, 939-41.
diseased subjects by a fair coin toss. Consicicr the example discussed in the enlly ror the ROC curve. The points on the curve IR given in the table.
area uncler the cwve SUmmary dIIIa ussd in an ROC CUIVB
Speciftcit)' I-Sensitivit)'
lolli-I
AUC -
2~(/i+I-li)tl'; + )";..... )
in many amIS or medical ~search. including bioc:quivalClltlC and pharmacokinetics. It pla),s an especially important role in the analysis of RECEIYER 0PERA1IN0 CHARAC'JERISIlC (ROC) CURVES. The area under lhe ROC curve of a diagnostic: marker (1Csl) measures the ability of Ibc I1UIdcr 10 discriminate between health)' and diseased subjects. II is the most commonly used measure of perfonnance or a lII8.Iler. We use the convention thDIlarger marlccr values ~ IIICR indicative ordisease. 11Ien if we randomly pick one subject rlOm the health)' population and one flOm the diseased population we would 'cxpect' that lhe value of the muter far the healthy subject would be smaller than thec:om:sponding yalue ror the diseased subject. AUC is the probabilit)' that this. in fact, occurs. The larger the AUC. Ihc bencr Ihc overall discriminator)' accurac)' of the marker. An Bra or I ~presents a perfect test while an IRa or 112 rqRSCnts a worthless test having a discriminatory ability. which is the equiyalent ofdiffen:ntialing between healthy and
'11tc AUe is used as a suml118l)'
measu~
0 0
0.56 0.04
0.14 0.12
0.94 0.32
0.98 0.60
1.00 1.00
11Ic data pn::scnted ~ult in an AUe as follows: AUe - 0.5(0.04-0)
x (0+0.56) +
(0.12-0.04)
x(0.S6 + 0.84) + (0.32-0.12) X (0.84 +0.94) + (0.60-0.32) x (0.94 + 0.98)
area uncler the curve (AUC)
This is a simple and useful mediad of obiainiDg a summary measu~ from plotted cIaIa. Medical research is frequently concerned with serial data. as in repeated measurcments (sec REPEATm MEASURB ANALYSIS OF VARIANCE) an a subject oyer time. e.g. blood aspirin c:onL'lCntralion mcasun:d at various times over a 2hour interval (Matthews el m., IWO). Sa)' we have n measun:ments y, laken at times II (i-I, ..., n). Such data arc tRqucntl)' cxhibited by plotting )'1 yersus I, and joining the resulting points by straight-line segments n:sulting in a ·curve'. The n:sulting an:a under Ihc curve (AUe) is often used as a single-numb« summary measu~ for Ihc indiYiduai subject. Further analysis of Ihc subjects or comparison or groups of subjects is carried out based on the summary measures. The AUe for the SCI of points (y,. I,) i - I ..... n is t),picall), calculalcd by the lnpCZium rule:
()'I) (I,)
+( 1.00-0.60) x (0.98 + 1.00») - 0.91 AD area or 0.9 I indicates the high discriminatory ability or the marker. For the ROC curve. estimating the area by the trapezium rule is equivalent to computing the Wilcoxon or MannWhitney stalislic divided b)' Ihc products of the sample sizes on the healthy and diseased populations. For smoothed ROC curves.. allemaliYe eslimates of the AUe arc available (faraggi and Reiser. 20(2). The effectiveness of aitemative diagnostic marten is usually studied by comparing their AUes (Wieand el a/., 1989). Adjustments of these ~u ror covariate infonnalion, selection bias and pooling effects an: discussed in Ihe ~fe~nClCs gi~n in Ihc entry for the ROC curve. Sc:histerman elol. (200 I) consider com:clions or the AUe for measurement error. For rurthel'details scc Hanle)' and McNeil (1982). DFIBR ........, D. and RII. ., B. 2002: Eslimalioa of the lR:a under the ROC CUI\'e., Slalulit'$ in Medicine 21.3093-106. HuIe)"J. A. and McNeIl, B. J. 1912: The meaning and use or the IRa under the n:ceiver opending clwKteristk (ROC) cun~ RlMJiolol)' 143, 29-36. ~........ J. N. s., A...... D. G .. Call1pIIeII. 1\1. J. and P. 1990: AIIalysis of suiaI melSU~meDts in medical rescuda.. BrilU/r Medicol JtHll"lJQl 300. 230-5. SdIIIt--. E.. ........, o.,Reiler, B.andTrmsan.M.200I: Statistical infamce for the ma under Ibc ROC CUJVe in die pmlCDCC of random
ItoJstaa.
measumaenl CI'RIf'. Am~rit.Ylft Journal of Epitkmiolol)' 154. 174-9. WIeaIId, Gal, l\L H., J ..... B... and J..... K. L 1989: A family of non-parametric stali.stics for comparinc diagnostic
s.,
marken with paimI or uapaimt daIa. Biometriko 76. S8S-92.
artificial Intelligence (AI) This branch of computei' scielK'e is devoted 10 the simulDiion of intelligent behaviour in machines. Traditional focus an:as of AI an: machine vision. MAOIINE lEARNING. natural-Ianguqe processing and speech n:cognilion. Historically an interdisciplinary field. and helK'e characlerised by the pn:scnce of several
17
ASSOCIATION __________________________________________________________________
competing paradigms and approaches. recently AI has staJtcd developing a more unified conccptual rramcwodt. based largely on the convergence of statistical and algorithmic ideas. A constant theme of AI Ihroughout its history has been 'pauem m:opition', Ihc cruciallask of delCcting "pa1lems' (regularities. relations. laws) within daIa. This task has elllCJ'Fli as a roadblock in aUIhc lladilional areas mentioned earlier and hence has aunctcd significant aucntion. Since most cum::nt approaches to pallern R:COgnition involve signiftcant usc of statistics. this has bc:come an important ~I in AI in general. Recently. AI has bc:cn applied to a new series or important problems and this. in tum. has hc:avily aJTc:ck:d general AI ~. Important applications of modem AI include: intelligcnt data analysis (sec also DATA MININO IN MEDICINE): information retrieval and filtc:ri~ from the web; bioinfarmatics; and computational biology. Tmditional application areas. by way of contrast. included lhc design of EXPER1' SYSTDIS for medical or indusbiDI diagnosis. me:thods for scheduling in logistics and creation ofoIhcr decision-making assistant software. The imprecise definition of what AI actually is has made it harder in time: to gauge the impact of this n:sc:an:h ftcld on everyday applications. A number of widely used computer programs would have met early definitions of artificial intelligence.. e.g. popular wcb-bascd n:commcndation systems or air travel planning advisors. Popular techniques for pallc:m n:cognilion such as NEI1RAL NETWORKS, clc:cision ~ and cluSlu analysis (see nUSI"ER ANALYSIS IN MmICINE) have made lhcir way into the standard toolbox of data analysis and are commonly found in lhc toolbox of any biology lab. Machinc vision methods are routinely used in analysing medical images. as wcll as parts of systems such as microanay machines far collecti~ gene expression data. Web retrieval and email filtering software also incorponde several ideas from natural-language proccssi~ and paIteIn m:ognition and Ihc modem sequence analysis of genomic data heavily relics on techniques originally developed for spccc:h nxvgnition. Intelligent web agents exist to find, assess and rclricve relevant infonnalion for the user and spc:cch-n:cognition systems are routinely used in automatic pbanc information systems. 111e field of artificial intelligc:nee has clearly produced a number of pnc:tical applications, but-lhc critics say - these have been achieved without solVing lhc general problem of building intelligent madUncs. Maybe for this n:ason, gc:nc:rally the main suc:ccss story of AI is n:ported to be the defeat of the chess world champion Gary Kasparov by an IBM algorithm in 1997. The origin of Ihc field or AI is often idcntified with a paper by A. M.1Uring. whichappean:d in 1950 in thejournal Mintl, and with a workshop held at Danmouth College in the
summer of 1956, although many key ideas had already bc:cn debated befon:, during lhc early years of cybcmc:tics. Modem techniques of artificial intelligence include Baycsian belief networks. part of lhc more general ftcld of probabilistic graphical models: pattern-recognition algorithms such as SUPPORT \'EtTOR MACHINES. which represenl the con\'ergence of ideas from classical stalistics and from neural networks analysis; statistical analysis of natural languagc tcxt and machine vision algorithms: reinforceme:ntlearning algCll'ithms which represent a connection with control theory: and many other methods. !VenDS BIIbop. c. 1996: Nellral nelK--orks jor pQllern recognilion. Oxford: Oxford University Press. Mllcbell, T. 1995: Mamine learning. Maidenhead: McGraw-Hili. R...., S. and NOI'YIat P. 2002: Artijit'ia/ inlelligen~e: a ",odem approach. 2nd edition. Harlow: Pn:ntice Hall. SbaweTaylor. J. aDd CrlsUanlnl, N. 2004: Kemel methods for pallerrr allQlysu. Cambridge: Cambnqe Univcnity Press.
association
This is the statistical depcndc:noe between two variables. Measura of association, unlilce descriptive statistics of a single variable. summarise thc extent to which one variable: inm:ascs ar dccrc:ascs in relation to a change in a sc:cond variablc. The basic graphical analysis of two variables is the SCA1TERPLGr. wbk:h provides evidence of association in the shape and direction of the seanc:r or points. In the example given here. there appears to be an association between bady mass index and systolic blood pn:ssure values in a samplc of a few thousand middle-aged men and women: higher values of body mass index lc:ad to be associated with higher \'alues of systolic blood pn:ssure.. suggesting a "positivc' association. A ·neplive' association. in cantrast, would dc:smbe a situation where an increase in one wriable: tc:nds to be n:latcd to a dc:cn:asc in lhc second variable. Various statistical measwa can be lRd to inlCrpn:t Ihc degn:e of association.
Correlatiorr c.oeffi~ienl. This specifically measures lhc degree of lirrear association between lWO quantitative variables on a scalc from negative one to positive one. A value ofzero indicates a total absence orlincar association. whilc a value of positive or nqativc one indicates a perfecl linear relationship. The correlalion coemcient between body mass index and systolic blood pressure in our example was 0.25, indicating a positive association that is less than perfectly linear. Howevc:l'. adherencc to a linear relationship is only one form of association and it is easy to imagine other plausiblc patterns of association. such as a parabolic scatter. in which the change in one variable: may be perfectly reftected in thc change in the second variable, but the correlation coemcient might be close to zero.
_ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ ATTENUATION DUE TO MEASUREMENT ERROR
Regreuion t:oejJicienl. In the cascofsimple lincarreg~ssion. then: is a complc:tc c;orrcspondcnce between the (."C)IKlation c:oeflicient and the regression c:oeflicient for the slope (/J). 1'11c: regression coefficient. thCRforc. also measmes association. but its value is interpreted as the magnitude of change in the dependent variable thDl arises. on average. from a unit chang~ in the independent variable. In our example. an estimate of fJ = 1.37 indicated Ihat a I kglm2 increase in the body mass index was associated with an average in~ of 1.37 mmHg sylllolic blood pn:ssurc. However. in more complex regression models, the regression coefficient can measure other forms of association beyond linear dependence. For example. either the dependent or independent variable may be mathematically transfonnc:d. such as raising to a higher power. taking logarithms, etc., and the association measun:d by the regression coefficient would express a nonlinear change in one variable in response to a change in the second \·ariable. Relllli.'e riJlc. In the special case of two binary variables. various nlio measun:s arc often used to quantify the degree of association. forexample. one variable might be a measure ofdisease OCCUI'ICncc:.the other a biolOgical or environmental quantity. Most commonly the ratio would compare probabilily of disease expressed as an odds. a risk or some olhcr relevant approximalion to the risk. A relative risk value of 1. indicDling equal risks in both groups. suggc:5Is that no association exists between the biological or environmental quantity and disease. If a statistical measure suggests posilive or negalive association. this should not immediately be taken to imply thal the association is valid and gc:ncraJisable. Several ~ siderations mighl lead us to question the importance of an observc:d statistical association. Firsl. considc:ntion of the STANIlo\RD ERRDR of the measure of association. generally re8ccting the size of the sample. places Ihc magnitude of association in perspective with the magnitude of random c:rror. Apparently shollg associations may in fact be poorty estimalc:d and fall short or SlAtislical signiflcance. Second. an apparent association may be entirely spurious (i.e. 'confoundc:d') due to the inftuenc:e of Glher measuraL or unmeasun:d. variables that hayc not been accounted for in the analysis. For example. in II IRliminary statistical enquiry. risk of coronary hc:an disease may appear to be associated with watching television. although consideration of the underlying relalionship with obesity and physical exercise would probably suggest that Ihc preliminary Onding was spurious. An association may alter after adjustment for the interdependence oroeher variables and Ihc gcnc:nl validity of a measa= of association would often depend on the extent to which such poICntial interdependencies have been taken into K-aJUnt. Studies measuring sevc:nl variables often utilise
multiple regression models to estimate adjusted regression coefficients and partial com:lation coeflicients by including all relevant variables in the model. However. even aIlc:r allowing for such intc:rdependencies. Ihc much strongc:r claim of CAUSALllY between two variables would generally require cxaminalion of more stringent CriteriL Third. an observc:d association may be speciftc 10 Ihc chosen range of the variables or to Ihc particular group of subjects studied and any inrerence beyond the range of the data to hand would require careful consideration of lite method of sample selc:ction. Various forms of selection bias may limit the ,eneralisabilily of the association. JGW
as treated
See INTENTJON-TO-TREAT
attenuation due to measurement error This is a bias reducing Ihc size of a correlation or a regression coefftcic:at due to imprecision of data measurc:mcnt. Consider an analytical epidemiological study in which the aim is to estimate lite CClItJI.EU.TKJN bc:twc:en true average consumption of alcohol (mg per day) and true a'lmlle systolic blood IRS~ (mmHg). Blood pressure measurc:mcnts arc wc:lIknown to be variable within individuals and a single measurement is likely to be rather imprecise (see J.lEASUREMfJO' FREaSJON AND RELLO\BWTY). Such a statement is even more true of a single day's intake or alcohol as a measure of Ihc true a\'CnIIC daily intake of alcohol (even if that day's intake wen: found to be measured without cnur). Now. in the c:pidemiological study we chose. ror each participant. to measure systolic blood pressure once and then ask them to recalllhcir alcohol intake the previous day. If we now calculate lite Pearson product-moment correlation bet\WCn Ihc two mc:aSUfCS we are likely 10 get a positive value that may be statistically signiftcanl (assuming we hayc a large enough sample) but will not be particularly high (i.e. not far above zero). Suppose, ror the sake of argument that we have found a value of lhis correlation 10 be 0.20. It should be fairly obvious that as Ihc measures or systolic blood prcs5ure and alcohol get less pteCisc (equivalenl for a nx.c:d population to lowering their reliabilities) the correlation will tend to zero. This is alIcnuation due to measuremenl erTOr. l.etlhc observed measurement of blood pressure for the 4h participant be Y, and the corrcsponding true average blood prcssa=be t'.. Similarly.lct the measured alcohol intake bcXt wilh a true 8\OCrage of",. We have estimated the correlation between Y and X. PYX. when we are really interested in Ihc corrclDlion between the lnIe w1ues. PII9' If the c:rrors of measurement for blood prcssa= are uncorn:lated with those ror alcohol consumption then it can be shown thDl Ihc rollowing relationship holds: (1)
19
ATTRIBUT~~SK
____________________________________________________________
HcM. "r and "Jt ~ the reliabilitics of the blood pleSAR and alcohol a1Dsumption mc:asuremenls respcc:tivcly. It follows that:
as good an cstimale as possible. especially when one employs anobscrvational study. Using BAYESTHE(IlEM and rearranging the cqualiDD. we can obtain an expreSsion exprasc:cl in tenDs of the relative risk (RR):
Provided wc know the reliabililies fCJl'the two measuremenls.
1 = Pr{EHRR-l)
this equation can be used 10 adjust Ihe observed atJRlalion between Yand X to obtain the required com:lation between their true average values. If we bow that "Jt I : 0~3 and ItJt=0.7. for example. the n:quin:d comdalion is 0.21 ,J(0.3 x 0.7) = 0.44. If. instead ofa correlation. the lincarregn:ssion coefficient for the effecl of blood presSIR on alcohol CODSumption wcre of key intelallhcn: (3)
and. again.1he n:quiml adjustmenl isstraightforwani. Equation (3) also holds approximately if we were 10 use a logistic rqrasion to pn:dict the presencclabllClltlC of hypertension. These calculalions are One as 10Rl as we ha\'C valid cstimates of the reliabilities. Howcver. Ihcy ~ only valid in these veJY simple situations as described. Epiclcmiologisls almost always wish to adjust their estimates to allow for confounding and some of these confounders an: inevitably goiRl to be prone 10 MEASUREMENT ERROR. Undel' these cimlmstances life is considembly more complicated! We cannot even be ccrtain that the estimate of the required parameter will be allenualc:d, never mind heine altenuated in a way described by equation (3). Readers ~ refClRCi clsewhere to these much mom challeRling but more realistic situations (Carroll. Ruppert and Stefanski. 1995; Cheng and Van Ness. 1999; Ouslafson~ 20(3). GO Carrol, R. J., RuppeJ1, D. and S......... L A. I99S: MI!tUUI'r,.nl ~rTtJf' in IIIHflinetlr motkls. London: Oapman " Hall. a..a. Co-L ..... Va Ness. J. W. 1999: StQI&tkal re,rrssiolr M'ilh IMtISII1'tRfMt e"OI'. London: Amold. CiuIIIIfIaa. P. 2003: MetlSUTr!-
,.nl ~"or and miNmsijitaliDII ;" stalistia tmtl epidemiology. London: Cbapmm" HalIlCRC.
where Pr(£} is the pn:valence of exposun: in the population at large. This is a COIlYCnicnl way of expressing the measure of association, because RR is often cslimalc:d usine alternative study designs. including C.~SE-CON1ROL. COHOIn' AND CIlOSS-SECIlOIW. SlUDIES.
Attributable risk is most easily inlClpretc:d when the factor of interest increases risk. i.e. RR > I. and in these cases the possible range of the measure is from 0 10 I. An altributable risk of zero can occur when no individuals in the: popuIalion ~ exposed 10 the factor of inlc:rcst. or if the: faclor is not relaled to risk of disease. RR = I. The measure is nol easily interpreted when the expos~ is proteclive. RR < I. so it isgenemllynot used in thisca5e. By n:cieftning the: reference graup. one can always cxpress the results of a study in a fonn in which RR is greater than I. so this is not a serious limitation. In addition. the lDCasure is oftcn expressed as a percent. As RR became large.).. goes 10 I. but A. goes 10 zero either as the proportion exposed. Pr{EJ. becomes small or as the relative risk. RR. appraached the: null value of 1. If an enlim population is cxposed to a particular faclor. Pr{ E} = 1. then the: sc:cond equalion (above) reduces to A. =(RR -1)lRR. The lable: shows a typical 2 x 2 tablc that can he usc:cllo display Ihe results from an cpidemiological study. In a casecontrol study. the column totals arc generally regarded as being fixed by design and the odds ratioorcross-produci mtio is usc:cl as a good approximation 10 the estimate of RR when the disease is rare. In addition. the exPOSlR distribution in Ihc conbols. Pr{E) = Pr{EtO}. is conside=llo be representative of the exposure distribution in Ihc overall population. Substituting in the samplc estimatcs ofthcse quantities gives rise to whal is the maximum likelihood cstimate of A:
attributable risk As a
mcaslR of the public health signiftcance of exposure to a risk factor for disease. the attributable risk provides an estimate of the proportion of diseased subjcc:tslhat may be allributc:d to the exposure. It is defined by:
A = Pr{D}-Pr{DIE} where PrID) is the probability that an individual develops disease and E and E reprellCllt whclhcr an individual is cxposed CJI' not exposed to Ihc factor of intcn:st (Levin. 1953). Ideally. one would like 10 know bath Prt DJ and Pr{ DIE} fCJl' Ihc population under study. bul for some study designs this is not possible. so if one wishes to use the measure, can: is needed to design a study that will proviclc
•
ad-be
1=---d(a+c)
attributable risk Results from an epidemioIogIcalstudy with two lwels 01 exposure and disease status Disetue slahU
Expo:mi
£
E Total
D
fJ
Tolal
a c a+c
b tl b+d
a+b c+tl N
_ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ AUTOMATIC SElECTION PROCEDURES
When selting a conllclcncc interval aboulthecslimale. Waller ( 1975) sugeSls using lhe: nonnaI appmximation an die log
transfonnalion of the complemenl of lhe eslimale: var[log(l-l)]
==~c(~tI:~C) + d(b:d)
Aliemalively. Leung aad Kupper (1981) have suggested using a IlIIil transformaaion ia which:
In a cohan study. the row IolaIs in lhe lable an: mgudcd as fixed: IherefCR such a study does nat provide a goad internal eslbnale of the exposure: distribution and neiihcr docs it provicle a good estimate of the IDIconditionai estillUlle or the probabilily or disease. In this case. the proportion exposed is usually cieri. rlOm aDOIhc:r study, perhaps an earlier caseCODlIol SIUdy or a survcy of thc entire papulalion. A CI'UlSsc:c:lional study provides both aD eslimale of the ~tive risk and the overall popuIalion distribution. so in that sense il is ideal lOr estimating altribulablc risk. However. a crosssectional SIUdy sutTen in other ways (see ~SErl1ONAL STUDIf.S). Wallei' (1976) discusses the: properties of eslimales of altribulable risk using these altcmalive study clcsilns. Melhocls for estimating attribulable risk far a particular expasun: while adjustiag ror potential canfouncling facton depends on whether lhe ctTect is conslanl oyer Ihe levels of the: covariates under consideration. When thc effect is CXIRstaaL it can be represented as having a cammon mlativc risk over the strata when using a stralified appraach. such as the Mantel-Hac:nszel method. or it can be IqRSCllled by a main etTKI only in a madel. such as the: linear IlIIistic model. la thesesilUations.onecandi~yusetheadjU5tedestimatoror
the: rOdive risk. along with an estilDllle of thc exlJOS'R distribution in the disc:uc:d &;rOup in lhe second equation (above) to obIain an eslimale oflhe adjustccl allributable risk (Waller. 1976: Gm:nlancl. 1917). Howcver. lhe assumplion thallhe associalion can be described withoulthe inclusion of an iateraclion lena is a sbung one and il is critical in thai a seriously biased estimale can result ir it is not 1nIG. An eslimale of altributable risk thai can be used eilher in a slnlifled aaalysis in which Ihc ctTect is nol homogeneous KlOSS slraIa or in a generalised linear model thai includes inlcraction lenDs can be exprased as: , - 1-~,,"'.. Pij
I'. -
RRlli
whcRj repRSCIIIS the levels of the faclOl(s) being actiusted. i n:prescmls the levels of exposure. Pu is the: propartion of diseased individuals in (IJ) and RR~ Ihe relative risk for exposure level i for individuals with levclj of lhe cowriales being adjusted (Walter, 1976~ Benichau. (993). TRH
or adjustment for cstimaIing the aaibutable risk in ellSC-CGllllOl sbDes: a new. Stalistics in Medkilll 10, 1753-73. Gnad.... s. 1987: Variance cstillllllOrl (or altributabk fractioncslilDlta. coasb1ent in bolla Iqe IUIIa and spanc cIaIa. SIIII&Iies in Medkiltt 6. 701~....... H. It. ... Kapper, L L 1981: CompariSCIII of confidence inlCmis ror atlributable risk. Biomelric. 37, 293-302. M. L. 1953: 'I1Ic OCCIIIRDCC or IURI cancer in IDIIL Alia Uni" Inlmltlli".lis CUll'", Ctllltrunr9. 531-41. W.....,s. D. 1975: 'I1Ic dislributiDn of Levin's IDC8RIJe of lllributable risk. BitJmel.62. 371-4. Waller, S. D. 1976: 1be cstimaliGll aad inlCqRIaIion orlllribulable risk in heal... 1aC1R:h. BitNnel,k$ 32. 829-49. ........ J. 1993: Methods
I.e.,
AUC
See AREA UNDER TIlE CURVE
autoconelatlon
See CORRELATION
automaDc selection proceclurea These an: p. . cedun:s far iclenlirying a parsimonious model in~ion in genc:nl and MULTDU UNEAR REDRESSION in palticular. Such methods arc needed because: in regression analysis an underfiacd model can lead 10 sevcmy biased estimation and pmliction. la conlraSl. aD overfilled model can seriously depadc Ihc efflcicncy or the: resulting paramc:IeI' estimates and pn:dicticms. Consequently a varielyoflec:hniques all wilh the aim or scleetiqlhc: mast important explanatory 'Variables far prc:dic:ling the response variable and then:by oblainiq a parsimonious and ctTectively predictive model have been developed. Perhaps the thn:e mast cammanly used melhods an: ft,,·...tmI .1«Iion, btldcBWd elimintlliDIr and a combination of bulb of lhese. known as sleplt'ise reSTeuion. The forward selection approach begins with an initial madc:1 thai conlains only an inten:epl and successively adds explanalcxy variables to lhe mode) from the pool of candidate wriablc:s until a SIaF is n:ached where none of the candidalc 'Variabl~ if added to the cum:at model. would conlribute inrcxmalion thai is Slalistically imporlaat concerniag the expc:cled valuc of lhe response. Tbc backward elimination mcthad lqins with an initial madelthal conlains alllbe explanaloly wriables being used in the study aad Iben ftnt idcnlifies thc single variable thai conlributes the least inranaalion aboutlhe expected value or the respanse: iflhis is deemed ROllO be "significant" then Ihe wriableiseliminaled rlOmlhccum:a1 model SlIL"CCSSivesleps of the melhad resull in • 'ftnaI' model from which no further wriables can be eliminaled wilhaul adversel), afrccling. in a sIaIislicai sensc.the pmliclcd value or the ellpected n:sponse. The stepwise n:gn:ssion method eambines elements or bath rarwanl sclc:ction and backward eliminalion. The initial madc:1 consi~d is one that contains only an inlen:cpl. Explanatory variables arc lhc:n consiclcn:d for inclusion in the CUl'lalI model, as described previously for rorward selection., bul now in each step of lhe procedure 'Variables
21
AV~LABlECASEANALYSIS
_________________________________________________________
included previously are also considcml for possible: elimination as in Ihe backward mclhod., and lhcy might be removed if lhc presenec of new variables in the model make Iheir contribution 10 pmlicting the expc:ctal response no longer significanL In multiple linear rcpasion lhc criterion used for assessing whcthu or not a Yariable should be added to an existing model in forward selection or remoyed from an existing model in backward elimination is. eS5Cnlially. the change in Ihe residual sum-of-squarcs produced by lhc inclusion or exclusion of the variable. Specifically in forward scJc:ctian an 'F-slatistic'. known as the F-to~ller~ is calculated as: F=
RSS",-RSS"'+I
RSS",+I/(n-m-2) when: RSSmanci RSS"'~I an: lhc residual sums of squares when models with m and m ... I explanatory variables ha~ bc:en ftued. The F-to-enter is Ihcn compaml with a pn:sct term; calculated Fs gJaICI' than the preset value lead to lhc wriable lIIICIu c:oMidcndian being added to the model. In backward selection a calculated F less that a corresponding F-to-remo\le lcads 10 a wriable being removed from lhc auRnl madel. In the stepwise proa:dure wriables are enaen:d as willi forward selection. bul after each addition of a new variable Ihase variables currenlly in lhc model are CXIIISidemi for remoyal by the backward elimination process. (For more details sec Petrie and Sabin. 2005.) In olher types of regmssion. for example. LOGIS11C REORESSJON. other criteria are used for judgiq whether or not a wriable should be enlcn:cl inlo or removed from Ihc: auRnt model. When applying rqressian techniques to HKIII-DiMENSION."'- DATA more sophisticated variable selection Iechniques are needed (sec. for example. Francois. 2008). None of chc automatic pl'OCcdura for selecting SUbsclS of variables is foolproofand it is possible forlhcm lobe seriously misleading in some circumslanc:cs (sec Agresti. 1996). That said. atlcast one can be more conlidcnl in a chosen model if aD thn:c procedures COIIYeIIt: on 10 the same sci of 'Variables. as OCCID'S quite frequently. bUI nul always. in pmctice. When dilTcmat subsets of variables arc indicated. judgcmcnt is ncccssary 10 decide on a prcfcncd model. such judgement being based on the desi..: to create a parsimonious model that is lilcely to be genenlisablc. not overly complex as if madelling mere quirks of the particulardatasct on which it is based. and yet inc:ludiq important OJ'standard paramctasdccmcd to be: of clinical relevance. SSE (Sec also ALL SlJBSETS RI3ORESSIO.~) Ap'estI, A.
1996: inlrotiJKliDli 10 tG/egoriml MIG QIlG/),Jil.
New York: John Wiley a: SolIs. Inc•• FraaeoIs. D. 2008: High· dilMlUiolltll dG/G antJlym:from oplinllli melrits 10/eGturr ~/t£ lion. VDM Verlag. Peart.. A. ... Sabia. S. 200S: Mediall JIG/ulits GI a gla,,~. 2nd edition. Wiley-Black'A~II. Chichester.
available case analysis This is an approach
to
multivariate data containing missing values on a number of variables. in which )dI!.AJIiS. VARIANCES and covarianccs (sec COVARIANCE MATRIX) are calculated from all available subjc:cts with nonmissing values an chc wriable (means and variances) or pair of variables (co'Variances) involYCd. Although this approach makes use of as much of the observed data as possible. il docs have disacb'anlqcs. For example:. Ihc summary slalistics for each variable may be based an different numbers of observations and the calculated yariancecovariance matrix may now not be suitable for methods of multiwriate Daalysis such as PRINCIPAL C'OMJ1ONENTS ANALYSIS and fAC'l1ll .o\N.o\LYSIS for reasons described in Schafel' (1997). (See also ttllSSlNO DATA. MULTIPLE D.lPUTA~J
SSE
ScIaaf'er.J. L 1997: Analysis o/illtOlllpkte muJl;J'tlI'iale daiG. Boca Raton. Florida: Oaapman.t. HaiLOtC.
average age at death
This lawed slatistic is someUmes used for summarising life expectancy and other aspc:cts of mortality. For example. Andcnc:a (1990) commcnlS on a study that campum average age at death for male symphony orchestra condUClors and for the entire US male papulation and showed ahat. on a'VCl1Jgc. the conduclors lived about 4 years longer. 111c difference is. however. IlIIIcly iUusory because as age at enlJy was birth. those in the US male population who died in infancy aDd childhood wen: included in lhc calculation of lhc average lifespan. whereas only men who survived long enough to become conduClors could enter the conductor cohort. The apparenl dilTcreace in longevity disappeared after' aa:ounliRg for infanl and pcrinalal monaIily. In Ihe other direction. a study in the USA that used average age at death of lUCk stan (which. on lhc basis of 32l such deaths, they round 10 be 36.9 yean) to warn of lhc perils of rock music also got it WI"Oq. It took no account of the rock stars still alive. Proper analysis of mortality inyolves the clcccnninalion of AOE-5FEC1RC RATES for mortality. which requires denominator data on chc agc distribution of lhc population (see SSE Colton. 1974). A......... B. 1990: Melhodolog;i.YlI erTtNs in metliml reswuth. 0xfCIrd: Blackwell Scientific:. CoIIOD, T. 1974: Stalistics in oWi"inr. Basion: Unle. BID'A'D aDd Co.
average treatment effect on the treated (ATT) See JlRalENSIlY scalES
average treatment eIfect on the (ATU) Sec PROPENSITY SCORES
untreated
B back-calculatlon Also known as back-projec6on,this is a nu:aas of esdmating. for example. put HIV infectioa raIes and pmlicqllle number of new AIDS cases in the rU1ll1e IUId was flm pmpased in the mid-.9. (BRIOkmcy~ and G~I, 1986). The esSCDCe.of the methad is contained in tM equation:
E s~ imated
HlIV incideTlce
/
I
J
d(I) == ;'(.r)p(I--.r)cI.r
o
where dll) and lIes) denole Ihe disease diaposis nIC III time , and the infection rate at time 8, and p(.) indicales the pmbabilily distribulion (density) of the illCu~on lime (or JNc:UBA1ION PERIOD). This eapression stales that Ihe rate of disease diapasis at lime I depends an the rate of new infeclions at time s and on die distribulion of the illCllbalion lime 1 -s.11x:..,f'om, ifanyawo oflhe~ IhreecampanenlS are kllOWD- Ihe third can be ;"forTed. Typically. the dilCUC diqDDsis rate for I up 10 the cum:ntlime T andlhe ~ bution iof the incubalion lime aM assumc:d known and the infection nile is estimated. The ftgaR explains the: idea in a discn:te time liamewalk usillllhc HIV epidemic as an example. ~.the intcn:st is in estimating HlY incidence and in PRCfictiDg rU1ll1e AIDS cases. Suppose data on new AIDS cases ow:r time up 10 the culmlllime Tare available IOgc:Iher with the information on lM distribution of the incubation time. It is then possible to ~t the nUlIlbel' of past infeclions that have resulted in the oba:rYecl AIDS cases. The estimalc:d incidence of HIV can be used in conjunction with the distribution of the incubation lime 10 produce short-term pmjeclions of neW AIDS diagnases. NOIc that in Ibis particular c:ase.1he MEDIAN Iqth of the incubation time is ofllle onIc;rof 10)'CalS, with very few individuals developinl AIDS within a short time period flUID infection. 1he observed AIDS cases thererCR provide information on infections that occumxl in the distant past~ raIher Ihan in IeClent years. &timalcs of incidence of infectian far IIIe yean JUII pn:ceding T will necessarily be quite inaccurate. as they are based on UllIe inrormation. Can: should Ibcn be: IDkcn in the inlc:lprdation or IeClent trends in the number of infections. HOMWer. this problem wiD ani affect pmjcctions of AIDS cues as long as they are short term.
C8leooar time
T
back-c:adculatloa Btlck-atlt'U/alion lain, HIV incidence lIIId F~dicl;on D/julure AIDS IXlSrS
A number offOlRlulations ofthe back-calcuJadon equation
have been JXCIPOISI'Il. To give a flavour or Ihe·cllimation problem. it is CXJRYenient 10 use a cIiscn:ac 'Version of our fint equation. Let 10 be die beginniq of the epidemic and)"1t the nmnber of individuals tIIal develop 1he disc:asc endpoint or inlcn:st (e~ AIDS in an HIV context) in the kth time inlerwl 1"-1. 'II;) for k =I •...• K. Suppose thai fu. Ihe probabilit)' or developing the disease endpoinl in Ihe jib time: inlervalgiven infection in the ith interval, is also known. Then the expected number of new disease cases in [tlt- .. Iv can be expn:ssed as:
Ir E(,.Ir) == LE(hiVII ;=1
wbereh,islhe unob&erved number ofnew infeclians in the.fth time: intuvaJ. Assuming thatlhe " an: independently di~ lributcd according to a PaSSON DJS'I1UBtmON wi'" panunc:1cI' E(hJ. then Ihe ,'ott an: alsO Poisson dillributed wi'" panunclI:I' B(yll;). F'mm this Ihe likelihood rar the obsc:nm data can be c:onstruclCd and maximised 10 obtained cstimales of tbc: numba-ofnew infections over timc (see MA.XBIlJU LlKELDlOOO DJmUBUDON).ln pnldice.eslimadon ofh=( h •• ... •/rll) is not so Slraighlforwani. The high dimensionality of b can lead 10 unstable c:&timates. In anIer 10 avoid lack or identifiability.
&rqdfllllllf6e CfMIJIIIIIflM I. MeIka'SI.;'1ia: S«'IIIIII EtIiIiM YIaI by Briu So Everitt .... ChrisIlClph« R. P'aIIaeI' C 2011 .folD Wiley ilk ~ Ltd
23·
BACK·~EcnON
......................................................................................................................................................__
some structun: ncc:ds to be imposed on the shape of II. This has typically been achieved by choosilll fully paramelric models for h-lI(q). The problem is Ihcn mluced 10 an eSlimalion of q, convenienlly ehascn to be of a lower dimension than h. AJlCmlllivcly. to n:1aiD some ftcxibilily, weakly paramdric models (i.e. step functions constanl O\'CI' a 10111 period of lime) ha\"e been specified or smooIhncss CIODSlnintson II havc been intnxluccd. 'nIis has CJaIcd a rich literature.. especially in the HlV ftcld (sec 8nxIkmc)'el' and Gail~ (994). AtlraCtivc in principle. givcn the simplicity of the idca.1hc mdhod docs rcquin: IRCdc knowlcclgc of III lcast two oflhc thn:e COmpaacnlS intmduccd aln:acIy. However, perfect information is ramy available. For cumple. as in Hay. Ihc incidence of the disease endpoint. typically acquired 110m surveillance schemes.. might be affected by reporting delay or uncIcnqJaniDg. FUJtIIer.lhc:dislributionofthe incubation lime may also be imprecisely known.. Results can be highly sensitivc 10 misspcc:ificalian of the iaputs.llislhcn:ftR impaltant thai data an: appropriately adjusted far delay in reporting bcrtR Ihcy ~ used in the back-calculation. Equally. it is esscnlialthat sensitivity anaIyscslO Ihc model chosen for Ihc distributiem of the incubation lime am carried out. One more limitation or the method is the inability to pmyiclc pn:dsc eslimalcsoftheineidcnccofinfc:ctioninn:ccnttimcs. Thisisa pallicuiarly serious problem for diseases with lang incubation limes. as seen in the HIVexample. These limitalions nalWitlulanc&ng. the back-calculalion mdhod has been wielely used and ~lopcd in various ways. cspcciaJly in the HIV an:&. Notably. the oriliaal methodology assumed a fixed distribulion for the incubation lime. independent of calendar lime or age al infection. Howevcr~ thcnpcutic changes Cft"eI' lime and the discovery of a clear dependence ofHIV progression on qe at infc:ctian havc made the tiJnc....qc inclcpc:ndcnce assumption untenable. This has led to thedevclopmcat ofagcHimc specific vcrsio. of backcalculalion. Equally. the need 10 CSlimaIc the number of individuals 81 difl'en:nl stap:s of the development of HlV has n:suItai in the devclopment of 'slageel' back-calculaaion~ whac the incubation lime is diviclc:d illlo stages according 10 the value of markers of HlV disease. A Rnal example is given by the need 10 rdlnccstimationofHIV ineidcncc. especially in rucnt years. and AIDS projections. This has n:suIted in a fill1hcr development or Ihc mcIhod. now able 10 iJlallPDr8le external informaIion on the disease spn:acI as well as oIhcr surveillance data. in addilion to AIDS diaposes (sec Dc AlIIClis. GiUts aad Day. 1998; Becker. Lewis and U 2003). The method and its developments have found important application in OIbcr contexts besides HlV.lhamplcs include the assessment of the bovine sponpfann cncephaIopaIhy epidemic in caltle and the CGDSCqUcal Crcutzfeldt-Jakob disease epidemic in humans in On:at Britain. the estimation of lhc Hepatitis C virus epidemic in Prance and the
estimation of Ihc in Australia.
DUmber
of new injc:clilll drug users
DDA
a.cctHttI, P. 1998: BlKk~aJcuJaticIa.1n AlmiIlP'. P. ancIColton, T. (eds).En"rlo'-ofbionatmicJ. \b1.1. Cbicheslcr:Jaha Wiley &. Saas.lJd.. pp.235-42. lder. N. G...... J. J. C...... U, Z. F. 2003: ~ific back-pmjeclion alHIV diaposiSditL S'alulirs in Met/kiM 22. 2177-90. R. .... Od, M. He 1986: Minimum size oflhe acquired immuaodelcieac:y syocIrome (AIDS) epidemic ia abe United StaICL Loner' 2(8519). 1320-2. lraak. ....,.....R.adO'O'M.H.I994:AIDSrpi#kmiolDrY:aqutmlitaiRte apprt1lldJ. N",,' YOlk: Oxfold Univenity PIaL De AaatUs~ 0 .. GIkI. W. R. ad DIJ, N. E. 1998: Bayesian pmjedioD of the acquimI immune deficiency S)'IICInJme epidemic. JDII1fIIII 0/ 1M Royal Slatislictli SlICi~I)' C - App 47. 449-81.
I......,.r.
backWards regl888lon
See LOCKSTIC RBIlESSION.
Mtl.11IU UJlEAR UDlESSION
balance
Sec RANDOMISATION
bar chart
A graphical display of data classiftccl into a nwnbel' of (usually unordcn:cl) cllleprics. Equal width n:ctangular bars ~ used 10 n:pacnl CKh calcgory. with Ihc hci&JIts of the ban beilll proportional 10 the observed fn:.qucncy in the com:spondilll category. AD example is shown in the lipan:..
200 0"1
€
E .sO ,~
:8 ;;;
....
tii 00
!;i,
~.....
;::.-,
0
50
:::!!;,
0
I II
I
I
I
.... cIwt MO"III;I,. rllle:l PI!1' 1000 live bi"hs,/oT rlrild,en
under Jive in./ire tlgJ'e1WII co"""ie:l An extension of the simple bar chart is the component bar chart (also known as the stacked bar chart) in which panicular lcagthsoreach bar am difTc:rcntialCd ton:pn:scnt a numbcrof
___________________________________________________________________ BARCHART
'Jbe basic bar chart is oRen of linle rnc:xe belp in undersannding catc:gorical data than the numerical data thcmselves. However. sophisticated adaptations of the graphic can become an extremely efTective tool for displaying a complex set of categorical data. Thai this is so can be illustrated by an example taken from Sarbr (2008) that uses data summarir ing the fDles of thc 220 I pnsSCDgClS on the Titani,', The data are catc:gorised by economic status (class of ticket. first. second or third. or crew). sex (male or female). agc (adult or child) and whether they s1Ir\'ivcd or not (the data an: available on Sarkar's websile. htlp:lllmdv.r-forge,r-projccL orgI), The first diagram produced by Sarkar is shown in the third figure, This plot looks impressive but is dominaacd by the third 'ponel' (adult males) as heighL" of bars represent counls and all panels have the same limits. Sadly. all the plot tells us is thal there were many more males than females aboord (particularly among the crew, whieh is the largest group) and abat there were even fewer children. The plot becomes man: illuminating about what really happencci to the passengers if the proportion of survivors is ploued and by allowing independent horixontnl scales for the dilTerenl
frequencies a5sociaacd with each category forming abe chart. Shading or colour can be used to enhance the display. An example is givcn in the second figure; here lbe numbers of patients in the four categorics of a response variablc for two treatments (BP and CP) ~ displayed. D IProgriE
2(]0
lPerliaJ r£t;3poose
.
• Comp1e1B rElqJ!llfl~
so , (]O
.50 0---
CP
BP
bar chart Response 10 IreDlnu:nI
Su rvived
No
Yes
0' 2004006:00800 J
l
J
.1
I
I
J.
Ch[ldl Male
.1
J
L
J
.1
I
I
.J
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Child female
I
1
Male
J
~ rn ~
~ ~
I
AdWt, Female
I
C rBW
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0 2004000006.00 ,
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~
; t
....
-
I I
I
I
~
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freq bar chart Srmmlll1',l' of Ih~ fDlr of fNJ.f,fengt:rs of IIU! Tilanic. cltuSijieJ by sex. Dge DnJ class (used "'ilh 1/." pemrisJ'ion of
Springer'
2S
BASELINE MEASUREMENTS _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ __
• I'd
OJ D 0 o 2'0
bar chart SUrI'il'al allumg diff('rtml suhgroupj' of Ptlsst'll..;ers on III" Titanic, willi a difftTml hori=OIrtal s('{II(' in eudJ panel (lI.\wl
"'ith
Ilr(' JWrnri,uion
of Sprillgt'r)
'panels' in the plot; this plot is shoYiIl in the fourth figun:. which emphasises the proportion or SUf\'i\'Ol"S within each subgroup ruther lhan the absolute numbers. The proportion of survi\'ol"S is lowest amon~ third-class passen~ers and the diagram makes it very clear that the 'women and childn:n first' policy did nOi work \'el')' we II ror this clas.... of passcn~er. (I am grulcfulto Dr Sarkar and 10 Springer ror allowing me to reproduce the Iwo diagrams.) SSE lSec also HlSTOORAM. PIE CRUlT)
Sarkar. D. 2008: u/tlice',' multiroriati.' data l';suali=lltion lfUh R. New York: Springer,
baseline measurements Thesc arc measun:menls taken al the bcgiMing of a study. (This section. however. concentrates on their role within the context of a CUl\lCAL TRIAL.) Baseline measun:ments come in different \'ariclies and rna)' aiM) ha\'C Il \'ariety of purposes (Senn. 1998). First are tif.'IIJClgraplri(· draractf.'ri.\'lic.'i of the patient. which either do not change (such as. for example. sex., change slowly. ir at all (such as heigh... or change Ilt the same rate for aU patients
(such a.o; age). The second and simplest sort is a measurement of the: same type as the outcome variable. but taken one or more occasions prior to RANDOMJS,\TION: these might be refem:d Lo as Iru,' base/int-.\'. l'bird. one ha.o; bas('/i/Jt' correIUlel·. measurements laken before randomisation on \'ariables other than the lrue outcome ..'ariable but pn:dicth'e of it and which ma), \'UI')' during the trial. Some such measurements are in\'ariably collected as part of the process or deciding which patients RUl)' cnter the trial. for cxample. it may be r'Cquircd in a trial of Ilsthma lhaL patients be aged 18-()S, have Il baseline fon:ed expinltor), volume in I second (I-'EV I) no man: than 75 tA of that predicted by age. sc:\ and height. can demonstrate 10 % re\'ersibilil)' ..... hen given a bronchodilalor and arc normolensi ..·c. Simply fulfilling these r'Cquirements will necessitate taking atlc.asttwo FEV l measurements prior to randomisation. as well as diastolic and systolic blood prcSSUr'C:!' Ilnd recording height. sex Ilnd a~e of patients. Lhe last two being variables that are always recorded anyway. In practice. man)' other things. such as. for example. concomitllnt medication and the centre in which the patient is trealed. will also be
_ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ BASELINE MEASUREMENTS
recorded and sueb thinp are also potential candidates for any madel. All thR:C kinds of baseline may be used for four further common purposes. First. to help characterise the patienlS iD the lrial; se:cond.. to CO!l1pllm Ihe groups in various arms of the lrials: third. to provide conditional estimates. which will generally have grcaIcr precision and will be conditionally unbiased given the observed baseline measu~ments; and fourth. to in\leStigate the constancy or othcnvise of the treatment elTect as patients vary. Tbe~ is a fifth purpose to which IrUe baselines can be put: as part of a general repeatedmeasun:s framework. such as. for example, the nndom slopes approach ofLainl and her c~wrilCn (Laird and Ware. 1982; Laird and Warq:. 1990). The following ~ some issues that arise:. Genera/ising rent/11 Using the actual baseline measu~menlS observed is clcarty superior to using the inclusion criteria to ebanclCrisc Ihe trial. as the latter simply define values the patients might have had. rather than values they did have. It is unclear. howe\lCr. to what exteat the baseline characteristics mc:asun:d can be used as a basis for ;encnlising the R:SUlts. since many lbinp that might be imponant have not been mcasun:d. In any case. the logic of clinical bials is comparative rather than ~praenlative. In many areas it is accepIed that the paticats in a clinical trial will be u~presc:ntative. b is hoped rather that an additive scale of measun:ment may permit use:ful application of the R:SU11s. 'l'bis may rcqui~ usc ofadditional covarialc information from the larget population (Lane and Neider. 1982).
Comparing groups. This su;;csts perhaps that Ihe sc:c::ond usc
of comparing the gmups is m~ valuable. Howe\"Cr. fJODl another point of view. the comparison of groups is simply an unimportant ~sting point on the road to adjustmenL If the baseline measu~mcnt is propostic a superior infm:ncc wiD be made by conditioning on it. whether or not it is imbabiac:cd. Particularly questionable is the common practice of comparing groups at baseline in lenDs of si;niftcance tests (Altman. 1985: Scnn. 1989. 1994). This has no uscftd role as part of a geneml strategy for analysis but could possibly havc some limited usc as a lest of the randomisation process itself (to detect fraud.. for example) as palt or some general quality control of the trial. That beln; so. however, the commaaly employed significance levels of 5 .. se:em inappropriate. COlYlrillle adjustment. This in turn sug;cslS that the third
usc of baseline measu~menlS. to provide conditional estimates by stratification or adjustment usin; ANALYSIS OF COVARIANCE. is the most important of these purposes. Howcver. many trialists appear 10 have a strong (one mi;ht
say unreasonably stron;) preference for simple analyses over mo~ complicated ones. ~fcning simple I-TESTS 10 analysis of covarianee and the log-rank test to PROPORTIONAL HAZARDS re;MSsion. Effects in ntbgroups. The founh usc of baselines is also
controversial. An issue of bias V.o\RlANCE b'ad~ofl' arises. Some. the ·splillers·, am ~ worried about bias and consider that it is important to report U"Catment effects by subgroups defined by baseline measu~mcnts; others. the ·poolcrs'. rqanl \'Driance as being the bigger concern and point to the unreliability of inferences based on small groups. Use t1f lrue baselines in repealed metUUres anal)'sis. A conbUversial maucr he~ is that the baselines an: sometimes explicilly measun:d as part of the outcome despite the fact that. obViously. the RabnenlS cannot affect the baselines. If the baselines. or some function of them. ~ also included as covariates this may lead to causally atlCCpIable infe~s. The simplest example is w~ change scores are used and baselines an: fitted as covariates. Infe~nces as to the elTcct of an:alment an: then identical to those that would be made using JaW outcomes and baselines as covarialcs (Laird. 1983). NOiflinear models. Far the ;encral linear model. the
cxpcclcd value of the estimator conditioning on the covariate is the same as the unconditional estimator. This is not generally lrUe for nonlinear cases. Gail eI III (1984) have CXJDSidcml where this docs and docs nol hold for a variety of models. Robinson and Jewel have concentrated on the case: ofLOOlSnc RECJl!SSION (Robinson and Jcwc:lll99l) and Ford ellll on the prapanional hazanls model (Ford ellll.• 1995). It is usually the case when: nonlinear models am involved that filling covariates leads to an inc:n:asc in wrianc:e. Ho\YCYCl'. the~ is a biasing of the lIaIment eft"ect towards the null if prognostic covarialcs an: nol flued. so it does RDI foUO\\' thal fltling such covariatcs necessarily leads 10 a 1055 of power. Then: an: many quments. in fact. as to why the conditional estimators should be pmem:d (Lindsey and Lambert. 1998). but so-called mallinal approaches using working com:lations malriees have also become exan:mcly popular. in particular via the OENEIWlSEDES11MA11NO EQUAlDI approach of Lian; and Zeger (1986). Measuremenl error. II is well known that whe~ a
covariate is measured with error. the estimate of ilS effect onoutcomeisatlenualed(SCCATII:NUA11aIIDUETOMEASlIItEME.W ERROR). The raise conclusion is sometimes drawn that undc:r such cin:umstanccs. analysis or covariance docs not yield conditionally unbiased estimaton (Chambless and Roebaclt. 1993). What has been overlooked is a
27
BA88UNEMEASUREMENTS _______________________________________________________ second aUenuation: dud of the InIC: baseline clilTerencc OD the obsened baseline difl'e~nce (Sena. 1994. 1995). The variance of Ihe observed covariate will exceed ahat of abe "Inle' covariate. The covariance of Ihe two CaD be shown to be abe variance or the true covariate. Hence. since Ihe n:pession of observed on InIe islhe covariance divided by Ihe variance of lnIe dais R:Jl'Cssion is I. HowcvCl'. the l"CIn:ssion of lnIe OR observed is the covariance divided by Ihe variaace ofobserved and hence is less than 1. On average Ihe IrUe baseline diffen:nce is closer to zero than the observed baseline diffen:acCo The two aucnuDlions euelly cancel out and so it IUrns out that corn:cting for an imbalance in obscncd covariales using the observed covariales is the right thing to do.
Correcti". .10' Ime IHJ.seline:.. It has also been claimed that. in the cue when: Ihe covari"e is of Ihe same kiad as the oulcome measu~~ iD other words is a true baseline. analysis of COVarillDCC is only appropriate if the baselines ~ balanced and that unadjusted change SCCRS provide an unbiucd estimate in Ihe mCR p:neral case (Liaag and Zqer. 20(0). This is incOll'eCI as lhe following eauntcrexamplc shows. Imqine a trial in hypertension in which. quite ilTBlionally. but as is theoretically possible, we include: oDly palients who have diastolic blood ~ssun:s (DBP) of either 95mmHg or I05mmHg (to the nean:st mmHg). Forty palients or each sort an: recruited and are allocated. otherwise at random. but in proportions 3: I in the Ilrsl stratum and 1:3 in Ihe sc:cond straIum. In Ihe absencc of any further bowledge. a pc.Jfectly aasonable estimate under Ihesc unn:asonable circumslances would be obtained by subtracting mea DBP under the active tn:atmcnt from mean DBP under placebo separalely in each of the twa strata and avcraging Ihe n:sults. Whal would be misleading would be to taIcc DBP at baseline from DBP al oulcome and com~ Ihe a'VCnlle over both slrata under active In:atmcnt wilh Ihat under placebo. Yet, since we can n:codc 95 and lOS to a dummy variable with valucs 0 and 1 by diViding by 10 aad subtracting 9.5, Ihe finl appmach is fOl'lllBlly equivalent to analysis or covariuce and the sc:c:ond approach is simply that of change-scon:s. Clroice of C'OIYlriIIles. Rcgulalor)o authorities an: naturally
ncnous that sponsors may unfairly muipul..e n:sults by choosing the model most faYDUrable to them and journal editon ouglll to have similar fears aboUI their authors. One way of prolCcling the 'J)"pc I CITOI' rate is to p~pccify the model. which is c:onunaD practice with abc pharmaceutical industry and n:collUl1Clldc:d by various guidelines (lntcmalional Confcn:nce on Hannonisalion, 1999). A modcl-chcckilll approach based on randomilBlion tests not using the tn:atmcnl infonnalion is an altemalive
(Edwanls. (999). Prom abc Bayesia paint of view, however. this is simply a formal and poindc:ss game. Having a \'IIIiable in a madel is equivalent to saying that one knows nothing about its effcclS. An excluded variable is one for which abc effect is known 10 be zero. Other posilions ~ possible. If uscn cannot which model is appropriate. Ihcn eVcn given a limon of prior ignorance: about the In:alment effect, diff~nl posIerior opinions will obtain. This may give a san or jullillcation for frequcntist SCDsiUrily analysis. However. il should nOl be folplten that whereas litlle may be known about the effect or In:aImcat in advance or a 1riaI. the same cannot be said for covariates. and such prior knowlc:dge is an imponaat guide: in the choice of model (Senn, 2000).
.RIC
Choice of lme btueline 10 fil. II sometimes happens thai in a IUn-in period a number of mcasurcmcats an: made: of the: eVCDlUal OUtcolDC variable. Often Ihe last only is used as a covariate. allhough this is in fact wasteful as it implicilly assumes. which is unlikely. an au~grcssivc process. II is beller either to fil the mean baseline or. m~ generally~ each of the baseline measuR:mcnls (Senn. 1997).
Subgroup tllllllysa tmd ITelIlnlmi by eo'",UJle Urfer-tlctions. Such analyses an: sometimes unclenakcn 10 cxamine the constancy of the tn:aImenl effects. The former islhe naaural extension or abc stratification approach and the lallel' of analy.sis or cowriance. Oace such uaI)'IICs have been unclcnala:n a pmbIcm or cambining results from individual 5Inda arises. This issue arises ft'cqucDdy in die: analysis of multiccnlM trials when: centn:-spccific efl'ccts may be examined. If such cffects an: wcighac:d by pn:c:ision. this is equivalenl to using 8AS 'I)pe II sums of squ~. If unweilhted avaap an: used. the equivalence is to 1YPC III sums of squan:s (OaUo. 200 1). Frana one paiDt of view. once an interaclion has bc:ea filted an overall effeCI is no longer or inten:SI, but it ca also be maintained that this llllitucle naively mainlDins abc claims or n:ducing bias against n:cIucing variance. Compromise positions involving random effects ~ sometimes used but not nearly as commanly in combiniDg effects from various ccntn:s as in the analogous problem in mcIa-analy.sis of combining eITects from various trials and hanDy ever when otha' IiOI1s of covariate an: involved. Gmd can: must be taken in inlCrpn:ling elfccts when intcractions ~ involved (Chuang-Stein and Tong. 1996) and it may be wise to fila model without interactions as a check (Scan. 2000). is recommended by international guidelines (lntcmalional Conf'en:al:c on Hannonisation. 1999). Nole ..... it is the interaction or cowriates with Ihe Raiment effect that causes problems in this way. The inlelaclion of covarialcs wilh each
nus
_ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ BASELINE MEASUREMENTS
other is not an issuc of the same impmtance. since it is mcn:ly the joint effect of these for which one seeks adjustment. or c:oune.lhere are also very many tc:cbntcal issues to be confronted when considering adjustment for baseline measurements. A particular inslrUclive case to consider is that when: a number. say k~ of binary covariates have been measured. One approach is thal of stratificaiioD. One CRates 21i strata based on these covariales. forms a tn:alment conlnlst within each and then a combinalion. usually weighted. of them all. In Ihe case of a linear model, if within-stratum variances are assumed constant and combined efficiently. this is equivalent to canying out analysis of covariana: using ordinary least squan:s having formed a faclOr for each binary covariate and fitting all mlCractions between covariates up to and including the highest. Nole that if we chamclcrise an inlenlclion by the number of cowrialcs r in~lved, with r= 1 corresponding to main effects and r=O 10 Ihe general inlerccpt. thea then: are in general (~) such lenDs and that since
t (~) =
21; one is filling Ihe same number ofdegn:es
offrcedom in bothcucs. as is indc:ed necessary. since the two arc equivalenL If~ are q treatments in Ihe trial, lining the treatment efTect as a main efTect only removes a further q - 1 degrees of freedom. Mostlrials Iua\'e two treatments and so q =2. q - I =1and onc: further*,," offn:cdom is removed. Ooing further and considering inlCl'aclions betwccn covariates and the treatment is mO\'ing a step along the road to splitling Ihe trelllment efTect by subgroup. Interactions between treatment and covariales will not be considen:d here and instead the issue: of intenlctions of covariates among themselves is consideml The approach via analysis of covariance has ~alc:r Hexibility than thal using slJata. since it is possible to fit the: main efTect of cowrialCs only or a limilCd degn:e or interactions between them. Funhcrmore. if we move to covariatcs with more than two levels. models with mluced degrees of freedom an: possible. Suppose. for example. thai we have measured baseline severity on a tllRe-point sc:aIe as 1. 2. 3. We can code this using two dummy variables. This is equivalent to filting a linear and a quadndic covariate. Possible schemes for both approaches arc illustrated in the table. Note thatlhese are equivalent since ZI =X2 + 2X:s - 1 and Z: I - 3X:l. 1he circumstances under which one would wish to fit Xl alone and especially X2, alone are fewer than those where one might choose to fit Z. alone. Thus. then: is an allrac:tive ftexibiJity and economy or the analysiS of covariance approach. or coune, where wly continuous measures arc involved the advantages for the covarialc modelling approach increase as arbill1U')' cut-points have to be used if slraliftcation is employed. SS
=
.....1IDe IDl8lllre.....1s Coding
sI..hemes for
a tlrree-poinl
se.wity xQle Dummy
l'llriable.s
Covariate!
Ilflert:epl Selrerily Sewrit,- Linear Quat/rQlic ielY!/2 level J Severity 1 1 2 1 3 1
X2
Xl
0
1
0 0
0
1
ZI -I 0 1
~
1 -2 1
AftmaD~ D. G. 1985: Compuability of randomized paups.. Slalis· lician 34. I. 125-36. CIIambItIs, L. E. and Raebaa, J. R. 1993: MeIhods for assessing dilfemtClC between poups ill change when initial measuremciU is subject to intra-individual \'ariatiOIL Sialis· lies in Meil;c_ 12. 13. 1213-37. a..q.s..m, C..... Taaa. D. M. 1996: The imp.:t of parametrization on the inlerprcblion or the maiu-elfcct terms in the pracnc:c or an interacliOIL Drug Infor-
DNJlion JOII17fal 30. 421-4. Ed. . . .~ D. 1999: Oa model prespccific:alion in confinnalory nmdomized SIUdics. Slalislia in MeJidlle
18. 7. 771-1S. Font. L a.L 1995: Modd inconsisaency. ill1lSlratcd b)' abc eox proportional hazards model. Slal;sl;cs br Medicin~ 14. 735-16. Gall, Me H.".L 1984: Biasc:destimatesof,"lIlmaIIe8"ects in randomized experiments with nonlineu np:ssions and omitted covariales.BiDmetrilca 71.431-44. Gallo, P.2001: Cc:ata'-'A'dpting issues in muhicc:ntc:r clinical mals. Joumal of Biophamrareu· liral Slatisl;cs 10, 2. 14s-63.............. CGnfenn&.oe GIl IIarnIcdsatIoII 1999: Statistical principles for clinical trials (lCH £9). Slalislit:s in Medicine 18, 1905-42........ N. 1913: Further campllratb'c analyses or ~1e5I posl-tcst R:SeBR:h designs. The Amen""" SlaJistidan 37, 329-30. LaIrd, N. M. .ad W.... 11'. 1990: Estimating rates of change in randomized clinical trials. Controlled C/iniC'tll TriaD 11.6. 405-19. LaInI~ No M. .ad \Vue. J. H. 1982: Randam-elfec.u models for Ion;itudinal data. Biometrks 38, 4. 963-74. LaM. P. W. and NeIder, J. A. 1912: AnaI)'sis of covarimce aad standIrdizaIion as ins1anc:es or pmlic:lioIl. Biomttrks 38, 3, 613-21. u.na. I(. Y. I11III Zeatr. S. L 1986: Lonptudinal daIa-aaalysis using generali7Jed linear models. BiDmetrilcQ 73. t, 13-22. ....... I(. Y..... Ztpr~ S. L 2000: Lonptudinal data aaaIysis of continuous and discn:ce n:spansc:s for IR1J05l designs. Sankhya - tht Inditm Joumal of S/alinia Series B 62. 1.34-48. LIndIey~ J. K. .ad ......... P. 1998: On the appI"OIIIiaIene or marginal models fClr ~ mea5lftDllents in clinical trials. Sialislies in Medicine 17.4.447-69. RabIIuoa, L. Do and JenD, N. P. 1991: Some surprising n:suJas .,.. oovariale adjusImeat in logistic n:pasiaa models./nlemaliono/SlatislimiRnieM· 58, 227-40. Sean, s. J. 1994: Testing for basdine balance in clinical trials. Slalisiks in Mtdicine 13. 17. 1715-26. SeIIII, S. 1995: Ia defence or analysis of covariance: a n:p1y to t1aambless and Roeback. Slal,,'io in Medicine 14. 20. 22I3-S. SlIm, S. J. 1997: Slaw/iral WMeJ in tbug derelopmtnl. Chichester: John Wiley &: So.... Ltd. SeaD,s.J. 1998: Baseline adjUstmelll in laagitw5nal studies. In AnnilaF. P. and CalIOU, T. (cds). Encyclopedia iii biMlalislirs. ~ll. New York: John Wile)' &: Sans. IDC., pp. 253-7. Sma, S. J. 2000: The many modes of mda. DnIg IrfonnaliOft JDlllflQIl4. S3S-49.
29
BASIC REPRODUCTION NUMBER _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ __
basic reproduction number A
Ienn used in the theory or infeclious diseases far the a\IenIIC number of secondary cases that aD infcctious individual pracluces in a allDpletcly susceptible population. The: basic n:pnxluction numbel' (R) of aD infectious agent is a key ractordetcrmining the mte of spread and the prapartion of the hOll population affected. 11Ic number- depends on the dumtion of the infcctious period. the probability of infecting a susceptible individual during one cont.:t and lhc numbel' of new susccplible individuals conlactcd per unit time; consequently. it may vary considerably for ditTerent infectious diseases and also for the same disease in dift"c:rcnt populations. 11Ic value of R has implications for whether them is a positive probability thai an epidemic may occur and the proportion of the population infccted 'WCM an epidemic 10 lake place. The largcr the value of R. the IBI'Icr the fraction of the popuIalion that must be immuniscd to JRYcnt an epidemic. A recent 84XlOUIIt ofthc usc ofthc basic repnx!uction number is givcn in Weslcy and Allen (2009). SSE
Waley, C. L ad Ala, L J. s.. 2009: The basic IqIIOduccion ....... in epidemic mcxIeJs with periodic demapapbics. JDlllflQlof BioID,iml Dynamics 3. 11~29.
Bayes'theorem Bayes' lhc:on:m is a mcthacl by wlUc:h conditional probabilities (see CONDmONAL FROBABIUTY) may be manipulatcd.1n particular. it provides a means ofn:vc:ning the conditioning in order to obtain pmbability statemenls rccanling spc:ciftc events of intcn:sI. Bayes' theorem itself was described originally in ·An essay ••• ' and published two yC81S after the dcalh of the Rcvcn:acl Thomas Baycs in 1761 (Bayes•. 1763). The: usc of Baycs' theorem in manipulating conditional probabilities is used widely. e\ocn ifusers may not be aware of it. but ilS use for rnon: general quantidc:s. for eumple relative risks, gives risc tocxmsidcrable controveny (sec BAYf.SL\N MEI'HODS). Following Spiegclhaller. Abmms and Myles (2004). COlIsieler two evcnts a and h. using the mulliplimlion I'IIle of JIROBI\BD..m"; Ihc probability of both II and b occurring, dcnoccd ·a 1\ b' is given by: 0
P(QAb)
= p(alb) x P(h) = P(hla»C P(a}
(I)
Rc:8I11IIIging this equation yiclds an expn:ssion fell' p(bla):
Combining equations (2) and (3) yields Bayes' theOMm. which expn:sscs p(6Ia) in terms of conditional probabilities far Q and the probability or h:
Pb _ P(tlJb} x PCb) ( III) - P(tJfb) x PCb) +P(Qlb) )C P(b)
(4)
Con\ocrscly. this equation could be considered in terms of b. i.c.:
b _ P(tlJb) )C PCb) P( III) - P(tlJb) )C PCb) +P(Qlb) )C P(b)
(5)
Dividing equDlian (4) by (5) yields:
P(bIQ) P(bIQ)
P(alb) x P(h) P(alb) x P(h)
P(alh) x P(h) P(alh) P(h)
(6)
Hence. equation (6) is Bayes" thCCRm in Icrms of the ocIds of event h. in which the prior odds of h. i.e. P(h)/P(b). an: modified in the light of the dala. i.e. the LIKELIHOOD RA11O.1o yield the pastcriorodds orh. conditional on knowing II. In the case when h is not a simple cvent. i.e. h or band b•• •• bIt an: in fact n mulUally exclusive cvenlS. equation (1.5) can be gencraiised so that the probabiUty of b.1II is given by: '0
Consiclerthecascofwishingtodetcnnincwhctbuapatiaat has a particulardiscasc. D. that the backcround pn:valcnc:c of lhc disease in the papulalian is 30 CJt. but a test is available. The: characlcristics of the test are such that a patient who has disease: D wiD lest positil'C with probability 0.8. i.c. the 5ENSI1M1'Y, while the pmbabilily of a positive tcsI result for nandiscased patients is 0.2. i.e. one minus the SFECIFICITY. Using Baycs' theorem we can calculate the probability thai a patient who has tested positivc docs hal'C disease D as:
peT + 10) x P(D) (DIT ) _ P + - P(T + ID) x P(D) +P(T + ID) x P(D) =
0.8 x 0.3 =0.63 0.8 x 0.3 + 0.2 )C 0.1
(8) (2) Considering theevcnts "II A b' and "II A b'. whcR b rcpJaCIIts theevcnt 'not b' • then these arc mutually exclusive and using the addilion nile of probability (sec probability). we can 'exlend the arpmellt' far II to include b:
P(a) =P(II1\ h) +P(IIAb) =P(lIlh) xP(b) +P(lIlb) x P(b) (3)
In terms of odds. the prior odeIs or having the clisc:ase are 0.31 0.1.0.43. i.e. just undcI-l in 2. whDe the IiIcc1ihaod ratio is 4 far a positive test result. i.e. 0.810.2. and the posterior odds or haVing the disease. having tested pasitil'C. is ~fan: 1.12. KRA Bayes, T. 1763: An essay lOWanis soIvine a pRlblcm in the daclrinc of chaaccs. PililosopldraJ TrtnuactiOlllo/tM Haytli Soc~ty 53. 41 B. ~, Do J., A....... K. R. aad Myles, J. P. 2004:
_ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ BAYESIAN METHODS
Ikl,..esilln apprDllt:Ms to dilrit:Q} Irillis and hmlth·C'tUe ~JYllUlltiOft. Chichester: John Wiley " SoDs. LJd.
Bayesian methods 1be use of Bayes' Ihcorem for manipulating conditional probabilitics of specific cvents of intcrest is used widely without conlrovcrsy (sec BAYES' 11IE(IlfJd). However. Baycs' lheon:m may also be applie:d to more gcneral quanlitics. c.g. relative risks. and in such scUinp the inclusion of e."Clernal information in the fonn oCthe unconditional probability distribution (sec CONDITIONAL PROBABLITY) for the quantity of intcn:st. the priordislribution. rather than the lRValcnce as in diagnostic testing. is controvcrsial and has altracted considerable debate (Spicp:lhallcl'. Abrams and Myles. 20(4). In short, a Bayesian approach (gcncnlly) has becn described as 'the explicit quantitDIi\'e usc of extcmal evidence in the design. monitoring. analysis. inlel]Rtation and reponing of a hcalth-care evaluation' (Spiegclhaltc:r, Abrams and Myles. 20(4). As such. it has been argued that a Bayesian approach is often morefIe."Cib/e than traditional mclhods as it can adapt to e:ach unique situation: is more effidenl in that it uses all available evidence thought to be relevant: is more ~I in providing IRdictions and inputs for making decisions about individual patients and summarising eYidence rcganling a proble:m. e.g. malting direct probabiUty statements that am clinically relevant: and more elhical in both claril'yingthe basis for randomisation and fully exploiting the experience proVided by past patients. There arc three clements of a Baycsian approach to medical statistics: subjective probability, assessment of eYidence and decision theory. Whilc the scaJIId is the one thai is most often thought of as a Baycsian approach per se, i. e.the use of extcrnal cvidencc. the first underpins many of the purponcd advantages of a Baycsianapproach. while the third iIIUslratcs the widerpcrspectivc that a Bayesian appn:Nlrh can give. A frequentisl view of probability relics on a long-nm view of the world. with probability being defined as the longrun frequency of events occUJring (sec PROBABLITY). While such a view is cntirely consistc:nt with replicable events. when considering unique evcnts. such as the probabiUly that a patient bas a particular disease. such a reliancc on repeatability makes little sense. A Baycsian approach views probability as a degrcc of belief in an event occurring, which docs nolrely only on n:pcalability but also encompasses a subjectiYC nature of probability. as wc all bring own experiences and background information in making probability assessments (Undley. 1985).1be use of a decision Ihcorclic approach to statistical infcrence plaecs the decision rcganling a paramc:tcr within the contcxt of the potential lossfgain in utility assoc:ialc:d with making dc:cisions (Lindley. (985). Fundamental in both frcqucnlisl and Bayesian approaches to statistical inference is the likclihood function (sec UKFlJ. Hom). From a frcqucnlisl perspective the likelihood function
summarises how plausible dilTcn:nt values of a parameter are by using an iR\'crsc argument. i.e. for a given wlue of the unknown parameter how plausiblc are the dala that ha\'C been observcd. A Baycsian approach uses the likelihood function. P( ),10). in the samc manner, i.c. as a summary of the relationship between data observed (y) and unknown paramcter (0), but using Baycs' thcamn reverses the: conditioning to obtain Ihc probability distribution for Ihc unknown parametCl' conditional on both the data and any background infonnation summariscd in the prior distribution, P(O). Thus:
P(Olv)
.
= P(O)P{)'IO) = P(.v)
1'(0)1'(.\'10)
IP(O)P(vt9}t10
(1)
Although this equation is applicable whether the modcl contains • single unknown panunc:lcr or multiple unknown panuncters. the speciftcation of P(8) (sec PRIOR DlSTRIBl1T1ONS) and the computation ofP(y) (sec COMPUTA11O.'W.MImIODS)can be more difftcult. but an addc:cI complexity is that we arc often only interested in cmain key pBl'llltlClel's. e.g. a treatment cffect, and wish to consider the OIhcr parameters as nuisancc parameters. Thus. in addition to obtaining the joint posterior distribution. we often obtain the IIfIlrginllJ posterior dislribuUon for one or more paramelcrs. say 8=(6• .;): then the rnarPnal postc:rior discribution for iJ is given by: P(6lv)
= Ip(81.l')d-tp
(2)
As with the: computation of P(y) in equation (I), Ihc intcgration out of the remaining model parameters in equalion (2) is very ran:ly analytically lraclable. 1bc prior distribution docs not necessarily have to be temporally prior to the study in question. but mthc:r is a summary of the pertinent external information, i.e. cither bascd on other studies. subjective beliefs or a combination of the: two. When there are multiple: SOIIKlCS of extcnaal cyidCIICIC in the form of other study Jaults. then the prior distribution may be based on a synlhcsis of such evidencc using meta-analysis or generalised evidencc synthesis techniques. which may downwe:ight some sourccs of external cvidCIICIC.e.g. observational studies. or may adjust the results for potential confounders or in order to make the synthesis of IIIOI'C relevancc to the study in question (Spic:gelhaltcr, Abrams and Myles. 2004). In 1CnnS0f using subjective prior belicfs. then: haw been a number of methods advocatc:d for the elicitation of such beliefs using a variety of methods. ranging from informal discussion. through the usc of structure qucslionnaiJa possibly using a "trialroulellc' fonnat to thc usc of intcractive computer clicitation techniques (Chalone:ret DI•• 1993: Spiegc:lhalte:r, Freedman and Parmar, 1994). When the beliefs of multiple individuals are elicited then ClDllsideration has to be given as to whether these should
31
BAYESIAN METHODS _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ __
be pooled in a ronnal manneroruscd inclcpcndently (Oenest and Zidek. 1986). A particular Iype or prior distribution thai is oftc:n used is what is termc:d a "noninformative' 01' 'vapelprior" distribution. Such a distribution is deemed to be "vapJe' relative 10 the likelihood so thai Ihe data from the study in qucstion dominalc the analysis. While such an analysis appeals 10 analysts wishing to maintain a sense of objectivity but nc\lClthc:lc:ss lalee advantage of GIber aspecls of adopting a Baycsian approach. e.g.1he ability to make direct probability statements. when considering prior dislributions ror parametcn in CXNDpiex models other than main cJTc:cts. e.g. variance components. can:f'ul considc:ndion has to be given 10 what "vague' rally means. and this should be assc:ssc:d as part of a sensitivity analysis (Spiqelhalter. Abnms and Mylc:s. 2(04). A related issue is that of whc:aher a "vap' prior distribution is inwriaDlto uansfonnations. i.e. what is vague on one scale may in ract be informative on anothCl'. and in sucb circumstances Jefl'~ys' priors may be considen:cl. which. allhough not necessarily "WlUC'. an: invariant 10 transronnaaions (Bemardo and Smith. 1994). In complex multiparameter models the specification of a joinl prior distribution can be a difficult task in itself. since assuming independence between all plll'8l11CteJS. and thus being able 10 speciry a series of univariate: priOl' dislribulions. is usually lIJIR:8Sonable. A consequence is thai we often have to spc:c:ify oonditional prior distributions. In summmy. then: is no such thing as a "CXHTeCt' 01' single prior distribution. and consideration or a range (or "community') of prior disb'ibutions is advocate:d (Spiegelhaltcr. Frcc:dman and Parmar. 1994; Spiege)haJter. Abrams and Myles. 20(4). Such a 'community' eould contain a "vague' prior distribution. a "sceptical' prior distribution, i.e. one that places only a small probability on an intc:nenlion being beneficial. an "enthusiastic' priOl' distribution and a prior essentially based at the null (Spic:gelhalter. Freedman and Parmar. 1994; SpiegeJhalter. Abrams and Myles. 20(4). Having obtained the posIcrior distribution using Bayes" theorem (I) all subsequcnt infen:nce is based on iL Standard measures of location and uncertainty may be obtained. e.g. posterior mean and variance. and the posterior density itself may be ploued. which is c:spc:cially important when it exhibits unusual behaviour. e.g. multimodal. CaEDmLE MER. VALS (Crls) can also be calculated. which IR analogous to CONFIDENCE INTERVAlS but which have the intc:rpn:tation often incom:ctly ascribed 10 Cis. namely that they IR intervals in which the unknown parameter lies with a spc:ciflc posterior probability. Crls can be obtained in a number or ways. either as equal-tail lIMa intervals or as highest posterior densily intervals (HPDls). which ha~ the property that no point outside the interval has a hi;her point probability than a point inside the interval and an: particularly informative when the posterior distribulion is either skew 01' multi modal
(Spiegelhaltcr. Abrams and Myles. 20(4). In addition to obtaining Cds. a particularly appealing advanlqe or a Bayesian approach is that direct probability statements can be made that a~ ofdirect clinical relevance. e.g. the pasteriOl' probability that a relative risk is abo~'e a certain value or is within a certain specified range (Spic:gelhaJler. Abrams and Myles. 20(4). Another adWDtage or adopting a Bayesian approach is the ability 10 make pn:dicti'VC statements rqarding future clata by obtaining Ihe posterior pmlictive distribution. The: posteriOl' p=lictive distribution for future clala is obtainc:d by inleglDling the likelihood function fOl' the future data over the posterior distribution. i.e. cUlMnt stale ofknowlc:dge rq;arding the parameter, so thai the pn:dicti~'e distribution for future data. x. having observed data y is given by:
P(.~I>·) =
J
P(·\"IO)P(9IY)dO
(3)
This equation can be: used spcciftcaUy in Ihe monitoring or sludies. since having obtained the posterior pnxlictive distribution. direct probability statements can the~f~ be made rqarding the eventual "observed' study ~sult and thus decisions made as 10 whether to continuc or not (see CLlNIC'AL TRL\I.S).
An allemali~'e form orthe predictive dislribltion is to use the prior distribution rather than the posleriordistribution and so the resulting pn:dictive distribution is in facl that fOl' the data observed. Comparison oflhis with the observed clala has been advocaled a means by which priOl'-ciata conflict can be: assessed. although this mises fundamental questiOns when subjective beliefs ~ used (Spiq:elhaJler, Abrams and Myles. 20(4). In many biomedical settings data accumuJates sc:queatially over time and an imponant advanlage in the use or a Bayesian approach is the ability of the Bayes' lhean:m to naturally accommodate such scenarios (Bernardo and Smith. 1994). Essentially. the posterior distribution at one time point bceamc:sthe prior distribution for the subsequent time point. assuming thai the data can be considered to be: conditionally independent. Thus. if data)". an: observed rust. followed by data )"2. then:
P(OI>·I.)'2) lX PlvIID)Pb"l19)P(9) OC P()rlIO)P(OL'·.) (4) Of fundamental importance to lhe practical application of Bayesian methods in a medical selting a~ the assumptions made regarding model parameters. In many situations specific model paramelers may represent subgroups of individuals within a single study (see SUBOROUP ANALYSIS). studies within a mc:la-analysis or units within an institutional comparison selling. Such multiplicity or panuneten requi~s assumptions to be made ~gardless or whether a frequenlist or Bayesian approach is adopted. From a
_ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ BAYESIAN METHODS BayesiaD perspective three possibilities exist: the parameten can be lhaught to be identical and therefCR all the data pooled and Ihc: commOll parameter eslimatcd: the parameten can be thought to be independent and lherefcn each subgroup/study/unit ualysed sc:parately (specif'ying an independent prior distribution for each); or the parameten can be thaught to be ·similar· in the sense that we thaught them nol to be systematically dirrerent. in which case they are termed "exchangeable·. If Ihe assumplion of exchangeability a priori is thought to be a reasonable one then the parameters are assumed to be drawn from a common distribution (with unknown hyperpanmeters) this specifics a hiel'llKhical or multile~1 model (sec MUJ.. TJl.£VEL ratODELS). Consequently. in estimating a specific: parameter. i.e. the underlying errect in a sUbpoupislUdyl unit. we ·borrow slrellgth' from lhe other parameters via the cammon distribution. ID practical terms. this means that a Bayesian approKh to problems of multiplicily ensllMS that individual parameters ~ shrunk towards some overall common effect and thatlhe "bonvwing of strength· ensures that there is less uncertainty surrounding the underlying effect within an individual subgroup/study/unil than had been originally observed in the data (Spiqelhalter. Abrams and Myles. 20(4). Specification of prior distributions for the unknown hyperpanmelc:n in the mocIcl then encompass the to which we belie~ individual subgroups/studiesl unilS may be differenl to one anaIher. As with statistical modclliq generally. model criticism can take the farm of msweriq thc:se questions: If a different statistical model were used would different conclusiOll be n:ached? How well docs the macIeI pcrfann.. i.e. how well does il madel the data? In terms of differenl IIatislical models.. obviously different models could be used and results compan:d or some form of model selection process may be usc:d (sec: later). Rcprding "model fit'. one approach is to consider pnxlidiCMI of the observed data based on the model and to compare this with the actual observed data using a cross-validation appmach to produce the: conditional predictive ordinate (CPO) (Oi!ks. Richardson and SpiegelhaJter. 1996). Altcmatively. an overall assessment of madel performance CaD be calculated deviance infannalion criterion (Ole) (SpiegelhailCl' el Qt•• 20(2). In addition. the use of specific prior distributions raiscs the question of whether diffcn:at conclusions would be drawn. legitimalely. by individuals holding diffcn:nt prior beliefs. However. sometimes equally impodant is the: specific speciftcaiiOll of PRIOR DlSIRIIlrIlONS even though they may be intended to be 'vague'. Consequcady. the use or a Bayesian approach dictates the nc:c:d far can:ful and coascientious seasilivity analyscs and this may appear daunting to the uninitiated anaIySL Model selection. whether n:lating to the speciftc parametric fona or covariales included in a model. can be
.,,.«
achievcdeithcr byquaJitalively comparing aspc:ctsofmodel lit. e.g. CPOs and DIC discusscd earlier orqlUlJllitatively via lhe use of Bayes' factors (Bernanlo and Smith. 1994). Bayes' factors provide a means of assessing lhc relative plausibility of the two competing models. in an analogous maDner to a UKEUHOOD RAllO. but havinl integrated over the prior distributioas for model hypcrparametcrs. Consequently, lhe speciftcation of improper prior distributions. which oRen arise when atlempting to repn:scnt ·vague· beliefs. causes compulational diflic:ullics (Bernardo and Smith, 1994). While Bayes' factors themselves can be used to com~ competing models dirccdy. and which do not have to be nestcd. they can also be used in conjunction with prior model probabililies to obtain the posterior model probabilities. i.e. the plausibilily of the competing models based on both data and subjective prior beliefs. and which can. in tum. be used to average DCIVSS models. so thatlhe estimation of a treatmenl effecL for example. takes into account both lhe within and bc:lwccn model uncertainty present (Kass and RaRery. 1995). As bas ahady been mentioned. the application or Bayesian methacls to realislic biomedical problems CaD be computationally intensive. with only highly stylisc:d examples beinl analytically trac:tablc.lnordertocvaluate inlqrals such as those in equations (I) and (2) lhn:c: broad techniqucs have been cunsidered: asymptotic approximalions. quadrature (numerical intepalion) techniques and simulaliCMI methods (Bernardo and Smith. (994). The development of MARKOV CHAIN MONI"E CARLO (MCMC) simulation methods together wilh usc:r-fiiendly software such as WinBUOS (see BlIOS .o\ND Vt1nBUOS) has caablcd the use of a Bayesiaa approach to be a realistic choice far many analysts regardless or philosophical crc:dcnce. n.e table summarises the differcac:cs bc:twc:cn a fftlqucnlist and a Bayesian approach to many oflhc: issues that arise in the design. monitoring. analysis and interpretation of RCTs and which are now discussed briefty. Although in practice Bayesian methods have been applied more fmauendy in the analysis of RCTs. use of Bayesian methods in speciftcally the design of early phase trails in which decisions as to the appropriate dose level or whelher to initialc a conftrmatory trial have to be taken as dala accumulates has received attenlion (Oalsonis and Greenhouse. 1992; Stalin. 1998). The role that elicilation of prior beliefs and demands from various stakeholders (clinicians. patients and policymakcrs) has to play in conftrming (or refUting) the need for a randomisc:d trial on the basis of equipoise has also been advocalcd. whether or not these are used in a formal assessment of whether a prvposed RCT is likely to lead to a definitive answer giveD the rcsoun:cs available and uncertainty in, for example. the event rate in the control group (Spiegclhalter. Abrams and Myles. 2004).
33
BAYESIAN METHODS _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ __ BayesIaD methods Comparison offrequenlul arrd Boyesitm DpprOtlmes 10 design, moniloring tmtI QIrtlI}-awmlerprelQliorr of RCTs (Qt/Qpled from SpiegelhQller. AbrQllfS Dnt/ Myles. 2004,
lute
Preqrlentist
BayesiQII
Extcmal information Sample siK
Infannally used in design Required to dc:tcct minimum clinically significant diffenmce at prespecified level or Type I and II enors
l'ararndcr of inlerc:st
Fixed stale of nature Justifies hypalhcsis testing
Used fonnally to specify prior Assumcdfixcd.. but assessment of probability of ftnal Cd excludin: clinically significant difference. allowing for unc:atainty in inputs Unknown quantity
Randomisation
Basic question
Pn:senlalion ofn:sullS
Interim analyses Inlerim pn:diclions Subsc:ls
Not neecsS8J)' due to subjective naI1Jre of probability How likely are How likely is value data given value of panmcler given of panamcler? data? Likelihood Plots of poslerior. functions. P-Yalues posterior probabilities or quantities and Cis of inten:st, Cds. posterior used in decision model P-valucs ad esti- Inference not mates adjuslCd for afTectc:d by number number of Daalyses of analyses Conditional power Use poSlcrior ~ dictive distribution Adjusted P-values. Subset cffc:cts 'sluunk' using e.&- Bonfemmi 'sceptical' prior
A crucial aspc:d of conducting large-scale PHASE III TRIAU is the issue or monitoring the trial as data accumulale in order to miDimiscexposure ofpatienlS to lesseffc:ctive (or evc:a hannful) interventions. From a fR:qllCDtist pc:rspc:ctive such monitoring raises issues of multiplicity and for which methods to adjust for this to exist. The usc of a Bayesian approach to accumulating evidence is entirely natural. in that aI various stages during a trial the posterior distribution for the outcome is an uscssment of the cum:nt stale of knowledge and on which decisions n:ganling continuation/ termination should be based without the need for
adjuSlment (Fayen, Ashby and Parmar. 1997). An additional advantage is the ability to pn::dicl. using the posterior predictive distribution at iaterim inspections. what the consequences of continuation would be: in terms of the eventual posterior distribution. conditional on the data so far (Abnms, 1991). An alternative approach that has been s",gelled extends the considc:ralion or the posterior distribution to incorporate the potential losses or making (SpiClelhaltcr. Abnuns and Myles, 20(4). One key question. however. is whal prior to use in such monitoring situations. As regards Ihc situation in which a difference in favour of one intervention has bc:ca ddc:ctcd. then a "sceptical' prior (see PRIOR DISl'RIB~) has been advocated. on the grounds that if Ihc data so far am suf6cic:at to convince a ICICptiC ofthc merits ofa particular intervention then continualion would appear inappropriate (Fayc:n. Ashby and Pannar, 1997). Similarly, when no diffen:ncc has been dc:tcctc:d at an interim analysis. aD enthusiastic prior disbibutionalUld be: used to DS5CIS whc:thc:r then: issuflicic:at eviclelaec for a proponent of an intervention 10 rule out a beneftt. Having conducted an RCT, how should the results be analysed and interpn:tecI from a Bayesian pcnpcctive and what advantages do they confer? Ultimalely, a Bayesian approach allows an exploration of how and why individuals interpn:ting the SIUDC ReT eviclelaec may n:ach differing conclusions - aamely thai they held diffen::nt a priori beliefs. although in the light or substantial evidence evc:a 'sceptics' and "enthusiasts' should conVCIJC to a consensus. 'J'bc usc or Bayesian methods also rocuses atlenlion on estimation and/or decision making and enables direct probability statements to be: made thai an: of clinical n::levancc. It also c:aables the inclusion of pertinent external infonnalion, which in Ihc case or ReTs that are relatively small, but which have produced I~ effects and appear to be 'too good to be true' • provide a means by which such n:sults can be: amelioratc:d (Spiegelhalter. Abrams ad Myles. 20(4). An altemalivc approach in such cilalmSlDnccs is 10 ask the question: Whal prior beliefs would 1 have to hold in order not to IICceptlhc findings or an RCT? If the prior beliefs n:quin:d to overturn such findings are so ·cxnme' that it is unlikely for them to be held by a rational individual then the RCT n:suIts an: accepted at "face value'. Fmauc:ady in RCTs. inlen::st focuses on subgroups of patients (see SUBOAIOOP ANALYSIS) and interpretation of Ihc effects of an intervention within such subgroups raises issue or multiplicity. A Bayesian approach 10 subgroup analyses considcnthe simultaneous aaalysis ofthc subgroups within a hierarchical modcI. in which a ·sceptical' prior distribution is placed on the degree to which the c:sIimaICS of effectiveness within individual subgroups differ from one aaothcr - a consequence of such an approach is that abemmt effects in relatively small subgruups of patic:ats are ·shruak' towards
_ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ BAYESIAN METHODS
a common overall effect.1he degree of shrinkage depending on bulb Ihc size of the subgroup and Ihc degn:e of scepticism exprased. Such an approach thus reduces the pollSibility that spurious findings an: accepted unwillingly. Bayesian approaches to Ihc analysis of ReTs Olhcr than two-group parallel clcsigns ha,'C also been advocalcd. including CROSS-ovER TRL\I.S" FACIalLoU. Dams and CLUSTER RANDO. !.IJSB) 11tIALS (SpiegclhuJlcr. 20(1). The growth of EVIDENCE-BASED MEDICINE and hcallhcare is basc:d on the systematic sean:hing for and synthesis of rc:scard1 cviclcnce. MetlHlJlalysis, the quantilalive paoIing of evidence from 'similar' studies. raises a number of methodological issues for which a Bayesian approach has been advocatc:d. The most fuadamcntal issue in mela-analysis is heterogeneity - statistical. clinical and methodological. Statistical heterogeneity refent to the study-Io-study variability in terms of the estimates associated with each study. When ex.c:essi ve statistical heterogeneity exists attempts should be made to explain it in terms of study- and patient-level covarialcs. but this is not always possible and so random effccts models. which allow for such hclcrogencity. arc oRen used (Spiegelhallcr. Abrams and Myles, 2(04). Estimation of the variance components within such moclcls can be problematic. especially when the number of studics is small and Bayesian methods have the ad,'anlale of not only allowing for the uncertainty in variance wmponenl estimates but also allow for the possibility of informative prior distributions on variance components based on other external evidence. Clinical heterogeneity refers to Ihc fact that different studies may have used diffemndoses. may have had different palient populalioos. e.g. in terms of age. and may have considered different comparators. In panicular. studies thai compare different interventions only provide indirect evadeacx: for other comparisons and the usc of multipanmcter e,·idenc:e synthesis methods within a Bayesian fl'BlDCWork ha,,'C been advocatc:d in order thatlhc approprialc conelalion and uncertainty is laken into account. A specific issue for which Bayesian methods an: ad"lU1iagCOUS is when baseline ,uk is considered as a possible treatment modifier. i.e. the event rate in the wnllol group. Clearly regression techniques have to allow for the correlation induced between the control group event rate and In:almCnt effect. which is most easily ac:cIOII1plished by using effectively a multivariate melD-analysis model. Such multivariate models can also be used when multiple or surrogate outcomes arc considered. Methodological heterogeneity often refen to study design and Bayesian methods fOl' the synthesis of evidence from a variety of dispandC sources have been developed. e.g. randomisc:d and observational studies. epiclcmiological and toxicological and qualitative and quantitative studies. Thc:sc methods can allow for both heterogeneity between different
soun:csofevidence and can beextcndcd to allow for differing levels of bias associated with different study dcsips and quality. Specific methodolOgical issues in EPIDEMIOLOOY for which Bayesian methods have been advocalcd an:: !.IEASVREMEm' ERROR. MlSSINO DATA and pharmacocpidcmiology. when assessing evidence on potentially rare but serious adverse events. One specific an:a of cpiclcmiology for which Bayesian and empirical Baycs' methods have been used ror some considcnblc time is SM1lAl. EPlDEAOOLOOY. in which interrelationships between gcogmphical an:as arc considered. 1he wmparison of institutions in terms of health oulcomes. often rcfem:d to as profiling. raises a number of methodological issues. most notably multiplicity and issues concerned with interprc:ting the outcome in individual 'units' that appear abenant and for which Bayesian methods have been applied. In ewlualing hcalthcarc interventions intcn:st often rocuses not only on clinical effectiveness but also on cosleffectiveness (see COST-EfRC'11VE ANALYSIS). with both clinical outcomes and resoun:e usc/cost data collected as part of the study. Methodological issues arise when analysing bulb outcomes simultaneously. most notable of which is Ihc conelalion between the two and for which Bayesian methods have been advocated. Although collection of both clinical and cost data within an RCT is highly desirable. such studics arcoRea ofrelalively short duration and extrapolation to the longer tcnn and 10 include other oulcomes is often required. Such eXlnlpOlation is most f..,quently achieved within a decision-modelling framework- which decomposes the intervention/disease pathway into a finite number of transitions or slates bcIwec:a which patients can move (sec DECLSION 1HEClRY and MARKOV CHAIN Mmm: CARLO). Decision models can assess cithu clinical or cost-effectiveness of competing interventions 01' policies, with different ports of the model being populated by either different SCJUKCS of evidence or the same source. e.g. study. by using a common metric for different health states, usually a utility or quality of life outcome (sec QUAUlYOFUFE MEASURaIENT). n.c key advantages thai a Bayesian approach confen on such models arc the ability to infer indin:ctly key model inputs on which there may be no direct evidence and allow ror appropriate soura:s of uncertainty and correlation in the model inputs. The development of economic decision models can alllO play an important role in identifying aspc:cts of the model (and therefore intervention/disease process) about which there is considerable uncertainly and on which fwther rcsean:h may nced to be commissioned. While the an=as of application above have conceatrated on epidemiological and evaluation studies, Baycsian methods arc beginning to be developed in oahu areas of biomedical n:scarch. most notably image analysis. time series and genetics. especially the analysis of gene expression data. 35
BAYESIAN NETWORKS _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ __
While the: usc of Ba)'esian methods in many IR8S of biomedical resean:h conveys numerous ",·anlagc:s. Ihcir use mauiJa can:ful and conscic:atious application. which places considenble emphasis on Ihc role of seMitivily analyses wilh rapecllo Ihc sllllislical modeL prior distributions and computational methods (see MARKOV CHAIN MONTE CARLO and BUOS and WinBuos). In onb 10 impm~ and hannanise the ~il1l of anaIyscs using Bayesian mdhods a checkJila1 SlI)v!sWQlch (SpiegelhallCr. Abrams and M),Ies. 2(04) has bc:cn developed. KRA A.......... K. R. 1998: Moailaring nmcIamised CGfttIolied trials PIrkinson's disease trial ilIUSlrates the dangers or stopping carty. Bril" MeditQl Joumtl1116. 7139.1183-4........... J.l\L ... SmHb, A. P. M. 1994: BayaitDr lheory. Cbicbcstcr: John Wiley a Saas.Lld.CIIaIaDer.K..C..... T., ........ T.A. .... l\Iatb,J.P. 1991: Graphical elicitalion of a prior dislribuliaD for a cliaical trial. Slalisticitln 42. 341-51••• P.l\1., AsIIbJ. D. ..........r, l\L K. 8. 1997: TulOriai in biosllli5tic:s: Bayesian daIa monitoring in clinicallrials. Sltllulk~ in Mrdkine 16, 1413-30. GafsaaII, C. ad GneaIIDaIe,J. 8.1992: Ba)'aian mclhods forPbase I cliaical trials. SlalisliaillMedidlre 1I.1377-19.G..... c.. .... ~J.1916: Combining probabilily distributions: a critique and 1ft IIIIICIIaIaI bibliograph)'(wilhdisalssion).SlalistialISdarte I, 114-41. GlIb, W. R., RIc...... S. .... SpItae........,D.J.I996: MtlTleo" • • Mo"te CtUlo methods iIr prtlttire. New York: ctaapmaa a Hall. K-, R. ad A. 1995: Bayes' flClOnl and modd UIICCI'lainly. JOIIIfItll of lire AmeriRlL'l Sttlli"irtli AMotitlliolr go. 773-95. 1JDdIey, Do V. 1915: Mttlcilrg _wortS. 2IId cdilion. Chichcstc:r: Jaha Wiley a Sons. Ltd. Panur. M. K. B., SpIeaIIIaaIttr. D. J. _ .........., L S. 1994: 1'bc CHART trials: Ba~sian design and monilGriq in practice. Sltll&lit~ ill Metlidne 13. 1297-312SpI••'h'1Ir. D. 2001: Bayesian methods for cluster randamized IriaIs with CIOIItiIBlOUS RSpoaseL Sltllulit:~ in Medin. 20. 435-52Splellla.lter. Do J.. AInnII, K. R. .... MJ.... J. P. 2OCN:
,..n;
Raft..,..
BII}'eJitm approtldws 10 dilrimllrialJ II11II heallh~lUe nmutlliOll. audacster: John Wiley &: Sons. IJd. SpIepIWer. Do J., FrIed....... L S. &lid ........., Me It. 8. 1994: Bayesian IIPPR*hes lo rudalDiscd trials (with dilCUSSion). JounItIl of1M RtI)YlI SltllUlical Sotiely Serie~ A 157. 357-17. SpIep-'Mer, Do J.. Belt, N. 0., Carla, 8. P. ad na ..... UDde, A. 2G02: Bayesian mea5IIIa or model complexity aad fit (wilh discussian). JOUffIGI oj ,lie Royal Slalistical Socirty B 64. 513-640........ No 1991: Sample size delcrminatioa for Phase 0 cliDical trials IIascd 011 Bayesian cb:ision theory. BionrelrkJ 54, 279-94.
Bayesian ..tworks
One melhod or delenDining whether or noI lO Slop Ihe lrial is that of pcnuasion probabilities. The: pcnuadc-lhopessimisl probabililY (PPP) is defined as Ihc posIerior probability thai lhe: new balmenl is beta than abe standard (Ralmenl. The pcrsuade-Ihc-oplimiSI probability (POP) is Ihc posteriar probability thallhe new lRalmenl is no be:u.:.. than the SIandanl. Prior 10 cammencc:mc:al of the: trial. IWo pairs or prior disbibulians for Ihe effectiveness or the standard and new (Raiments an: chosen. One pair is thai of aD investigator who isoplimistic thalthe new tmdmc:al is beller than lhestancIanL The olhcr pair is that or someone who is pessimistic (ar sceptical) aboulthe effectiveness of the new balmenl. Also pn:-specified an: thn:sholds PPPCIUT and POPcarrAl each interim analysis PPP and POP an: calculaled using Ihc data colleclc:d so far. If POP> POPc ....,. Ihe trial is stopped. because even an opIimist should be penuadc:d that the new lreatmenl is no beUer than the staadanl. Similarly. if PPP > PPPcarr. the biaI is slopped bc:c&usc e~ a peuimisl should be: pmsuacled thallhe new tn:allnent is better. For further delails see HeiljaD (1997). SRS (See also Ba\YESJA.~ ME11IOO5J
HtItjIuI, D. P. 1997: Bayesian interim analysis or Phase I( cancer cliaical trials. Sltlli"icJ in Medicine 16. 1791-802.
benchmarking This is a proecdun: for adjusting a less n:liable series ofobservations to make it c:onsisIcnl with man:: n:liable mcasun:ments known as benclrnJtlTle,. For example. data on hospilal bed occupation coUc:cted monlhly will DOl necessarily ~e wilb ftgura collc:ctc:d aDnuaily and Ihe monthly IIgura (which an: likely 10 be less ~Iiable because the annual 11l1Ircs will pmbably originate from a census, exhausli~ administrative n:conls 01' a iarJer sample) may be: adjusted al some poinllO ap:e wilb the I11CR n:liable annual fil1lRlS. Benchmarking isotlen useclloacljust time-series dala 10 annual bc:ac:hmarb while pn:scrving as far as possible Ihe monlh-to-maath movemenl of abe original series (see. rar exampl~ Cholelle and Dqum. 1994). SSE CIIDieUe, P. A. ad ........ £. 8. 1994: Bcnclunartiagtimc series with aUlocondalcd 1illlYC)' cnors./,,'emtlliolloJSialislic,Rnk..·fil. 365-77.
See OIlAPHICAL MOIlELS
Bayesian persuasion probabilities These
Berkson's fallacy
1ft
posterior pmbabilitics Ibat a new lreatmenl beil1l lelilc:d in a Phase II clinical lrial is beller dum or no belle.. than a sIaDdanIlmilmenl.1n a Phase II lrial IN1ERIM AN.UYSES 1ft carried oullO dcaennine whether ar nolto Slop Ihc bial early becaus~ on Ihc basis of the dala aln:acIy accrued. the: new IMalment appears eilher unlikely 10 be beller than the slaDdanlllallDenl or alikely nollo be: better Ihan it.
Sometimes a spurious n:lationship can beconcluclc:cl because the dala from which the conclusion was clc:riyed came from a special soun:e, which is DOl repn:sentative of the gc:aeral population. Such bias is known as Berkson·s fallacy and it can anly be avoided by ClRful Slud), design (Waller 1980; FeinSlein. Walter aad Horwiaz.. 1986~
Woodward. 20(5).
A classic example of this bias is the study or aulopsies by Pearl (1929). Fewer aUlopsies dian expecrm found baIh
__________________________________________________________________ tuben:ulosis aad cancer lo occur together: the frequency or cancel' was thus lower among lUbcn:ulosis viclims Ihan oIhc:n. This Ie:d Peart to the erroneous eonclusion that tuben:ulosis might be offering people some kind of protection againsl cancer. even leading 10 the suggestion thai caneer patients might be lJ'eated with the protein of the aubeR:ulosis bacterium. 11Ie problem wilh this line of Ihinking is that DOl ever)' dcaIh is aUlopsied; in this case it turned aut that people who died with both diseases we~ less likely to be autopsied. leading to an anificiallack of numbers with both diseases in Pearl~s autopsy series. Bedcson's fallacy is a particular problem with caseconlrol studies. For example. suppose that both the case and eontrol series arc derived fiom hospitals. If it happened that anyoac with both the 'case' disease and some other disease we~ more likely 10 be hospitalised than someone with only one or the pair, we may well se:e a n:lationship between the p~valenc:e of the: two diseases in the caseconlrol study. even when Ibe~ is mally no such n:lationship in the general population. Exactly Ibe same situation may also give rise 10 spurious ~Iationships between any risk factor for the "second' disease and the disease that deftnes cases. For instance. consider a hospital-based CBSe-aJlltrol study of eoffee drinking and angina among the elderly. Suppose that coffee drinking is a risk factor for ParkinSOll's disease. If someone has Parkinson's disease she or he is unlikely to be hospitalised unless she or he develops a polentially life-thn:atening condition. such as angina. Most individuals with angina will be tn:ated in the community. the exception. perhaps. being when there is a disabling CDmorbidity. The ~sull of these hypothetical eonditions might be a disproportionate number with Parkinson's disease (who tend to drink eoffee) among the angina cases in hospital than among the controls (people with other iUnesscs). 'nle cusc>control stud)' would thus find coffee drinking to be a risk factor for aDgina. even if this wen: not ac~b~ (See also BIAS IN OBSERVA11CNAL SI1JI)IESJ
~
Felatteln.A. R.. Waiter.S.D.aadHorwUz,R. L 1986: Anaaalysis of Berkson's bias in casc-contrul studies. JOIITfIQI 0/ CIrrotr;~ Dis· elJSeJ 39,495-504........ R. 1929: Cancer and aubcn:ulosis. NneT;~Q11 JournoJ 0/HygieM 9, 97-159. Walter. S. D. 1980: Berkson's bias and its coatrol in epidemiological studies. JOUl'INII of Cluonk Disetues 33. 721-5. Woodward, M.2OO5: Epiden,iolol)': study, design llIfIl datil tIIItIlysis. 2nd edition. Boca RalOn: Chapman .t HalIfCRC PMs..
beta dlatrlbuUon This is a flexible PROBABJUTY DIS11lJ. BU11ON. eommonly used 10 describe a proportion. Whcn:as
many of the distributions we encounter arc nonzero OVCl' an infinite range of values. the beta distribution is nonzero only in the range 0 to 1. By n:scaling, it can be useful any time that a dislribution is required OVCl' a finite nmge. The dislribution
B~
is defined by two parameters. ,. and s, and has the density function:
j(.\")
= .t'-I(I-x)'-I/fJ(,.,s)
whe~ the fJ(,..:s) term CaD be viewed as a coMtant to ensure that the total probability is equal to 111Ie ~IEAN of the beta dislribution is r/(r+.r) and the
is ,..rI([(r+oJt(r+s+ I)]. The panunclCn r and s define the shape of the distribution. This shape can be wide ranging. with u-shaped CUI'\'c:s. n-shaped curves. sbic:lIy increasingldec~ing curves and lriangul., distributions all possible. Some or the possible distributions ~ illuslndcd in the figure (see pace 38). If,. and s ~ e:qual then Ibe distribution will be symmetric. Nole the similarities to the BlImMJAL DJSTRIB1J'I'ICN. W~ the binomial models the distribution or the number of successes, when given the probabiUty of a success. the beta can model the probability or a success given the number or successes. Indeed, in a Bayesian analysis (see BAYESIAN MEIlIODS), the bela distribution is the conjugate prior for Ibe binomial distribution. 11Ie bela distribution is n:lated lo a number of other distributions. It contains the uniform distribution OVCl' (0,1 Jas a special case (when r I and oJ I), it is i~ingly well approximated by a NORMAL DlSTRlBU110N as ,. and s increase and it can ~sult from constructions of the fonn AI(A + B) w~ A and B ~ both random wriables with OAMralA DlSlRIBurJONS. For furlbel' details on how the bela distribution ~laIes to othcrdislributions. see Leemis (1986). 11Ie bela distribution is most commonly used to model proponions. Suppose thai we wish to eslimale the specificity of a test that in trials Corn:dly identifies SO of the 52 participants that do nol have a eondilion. 11Ie usual normal approximation will not suffice since it leads to an interval rrom 0.91 to 1.01. and a value grealCI' than I makes no sease. 'nle~ ~ a numbel' of ways to use the beta distribution in estimating the interval (see Brown. Cai and DasGuplD. 20(1). AGL VARIANCE
=
=
DuG...,.., A. 2001: Interval esti-
Bro.... L D.~ C.., T. T. aad maIion for 8 binomial proportiCIJ.
Sltltisl;~ol Sdmce
16. 101-33.
Letads. L M. 1986: Relationships among common univariate distrillulions. The AnwritGII SIaiislidGII 40, 2. 143-6.
bias
Any experiment, sludy or measuring process is said to be biased if it produces an outcome that differs from the ·truth' in a systematic way. Bias can occur aI any staae of the ~sean:h process fmm the litcralU~ nwiew through to the publication of the results (Annilage and Colton. 2(05). It is important to dislinguish between bias or systematic error, on the one hand. and mndom error, on the other hand. For example, suppose that we had a population of subjects with a MEAN weight of 80 kg and a STANDARD DEVlA110N of
37
~----------------------------------------------------------------------
1
(.)
(b)
1.
1.5
.-t 1.0
10 •
,s. 8·
f
.i
8· 4.
.-8
~
.. 0.5
IM-t::::=t===::;:::==:;:::==r==::::;==::::t:===I 0.0
0.2
0.4
0.6
.0.8
1.0
I :-~~;;;;;;;;~;;;;;~J='===I 0:0
Proportion of success BS
12.0
r~
ti
-8 1.0
.-
~
0.0
0.2
p.4
0.6
0.8
(8)
.1
r.I.8.0.&
c: 10
8
t
6
i
0.0
0.2
0.4
0.6 0.8 Proportion 01 successes
1.0
r......
(f)
8 --------
a 6
I
• I· I:~~~~~~~ 'V
1:0
-t:::=t==::;:::::::;~:::;:=::;:::::::~::1
M
1.0
Proportion of SUCCBSSBS
t.
·0:8 0:" . Proportion·of SUlXl!sses
t
1.0
•JM-t::::~==::;:::==:;:::==r==::::;==_===1 I a·
0.4
(d)
(c)
~.
0.2
4
0.0
0.2
0.6
0.8
1.0
Proportion of SUCCI! SSBS
~
4 2 o~=*==~==~==~~~==~~ 0.0
0.2
0.4
0.6 0.8 Proportion 01 successes
1.0
..... dlltrlbaII_lliw"tl'ing Ih. rtII'illy.offomu I/rtl"lre wltl dUlr/buIID" can I.e: (II) lhe IIl1i[o1'm dillirilnll;on oJW (41). (h) tl hiniodtJJ CDMIIIV! .,,;bIIl;OII fin IIrU leJftey·s prior), (c) II t:UlW wil" tl sing/. made, (d,1I ~ jrlllClion oll~e proptll'liDll, fe) 1I11D111imN1,bul slill slricll)' inCf't!tl.fillg dUlribulion. UJ 1m eXlIIIIPl. Ihtll ill well tlpproximllled ~ ,he IfDrmtll dis"",,,lion
CAre'"
10 q. It we select • simple raDdom sample of·2S ·sUbjects tiom this popullllion and measun=lhcir weapls uliBl a wellc81ibnled sc:I of scales, l~ ·it is passib1e dual the IDeaD. weight far Ibis sample will be substantially cliftCmd. ftom 80 Icc. In fact. ~ is about a 1 in 20 chance: that the sample mean will be: IIIDRI than 4 k, below or 411 above the InIe mean or· 80 kg.
However, simple nndom sampliBl prod~ an unbiased e:&limale of lhe lrUe me&n weipt because:, if the pmcc:ss or sc:JectiBl a ~implc: IDJIdom sample: of 25 ~bj_ and compulinglhe sample: mean weight werelqle8led a Iaqc: numlJc:r or limes. the distribution or die: sample: means be: cc:nlml arvuncIdIe IIUe mc:an of 80 kc. 11K: larpr die sample ~ dac: closer Jhe samp~ mc:aas will be: clllltc:led around
wau"
_ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ BIAS IN OBSERVATIONAL srUOIES
the true populalion mean. In alher words. the cxpected value of the sample mean equals the populalion mean. In this sccnario, there is no bias and any deviation of Ihc observed sample meaD from the lrUe value can be accounted for by pure chance. known as nmdom variation or random C:II'or. If. howevcr, the weighls of a random sample of subjects were mc:asunxl using a poorly calibrated scl of scales that weighed each subjeci as being 2 kg heavier Iban Ihe actual weighl. this would lead to a biased estimate of Ihc lIUc population mean weighL The six oflhis bias. or syslemalic error. would nol be by incn:asing the sample size and the distribution of the sample mean will be ClCnln:d around 82 q nlher than 80 kg. 11ae systematic error in this example is a mc:asun:menl bias due to a faulty measuring instrument. More genc:rally. measu~mc:al bias could be due to such diverse causes as poor queslionnaire design. faully equipmenl. obsener enor or n:spondenl enor (Silman and Macfarlane. 2(02). Examples of observer error include mi~ading the scale on an inslrUmc:at. bias in reporting results by an unblinded ewJuator in a clinicallrial or bias in eliciting information aboul the exposun: histol)' of c.asc:s and controls in a CA5E-cDNl'ROL SI'UDY. Eumples ofn:spondenl error include biased reporting of symploms by unblinded patienlS in a clinical llial. bias in rc:call of exposwe histol)' by cases and controls in a case-conlrol sludy (sec BIAS IN OBSERVATIONAL S1\JDIES). All types of study ~ susceplible to design bias. This can arise from many sou~es. such as saEcrlON BIAS (when the subjects selected for study ~ not relRscntalive of' lhe target population). NOmlBI'ONSE BIAS (when there is a systematic difference between the chanc:leriSlics of those who choose: to participate and those who do not). IlODComparability bias (when groups of subjects chosen for comparison in. for example. a c.ase-conllOl sludy are not in fact comparable). Randamised trials (see aJNICAL 1RJALs) arc genc:rally ~gardcd as being leaSl susceptible to design biases. 'I1Ie scope for BIAS IN aBSERVAllONAL SnJDIES. especially case-control sludies. is much greater. Annitille and Collon (2005). Ellenberg (1994). Porta and Lasl (2001) and Sackell (1979) all proVide a comprehensive descriplion of so,""s of design bias. Analysis bias arises from emn in the analysisof'dalL This covers such issues as confoundilll bias (in which conrounding fadars have nul been approprialely adjusted for in the analysis), analysis method bias (includilll inapplOpriale assumptions about the distribution of wriables. faulty strategies far handling MlSSIND DATA ar otmJERS. unplanned SlJI. OIOUP .UWoYSIS and dtlltl dredging) (Annitille and Colton. 2005; Da\'ey Smith and Ebrahim. 2(02). Ensuring that the interpn:talion ofdaaa is unbiased isjust as importanl as ensuring Ihat the pnJCCISCS of design. rnc:asuremc:nl and analysis arc unbiased. Bias in Ihe interpretation or data can be conscious or unconsciaus and is padicularly
rmuced
dimcullto adcIIus because it involves subjective judgements on the part of the reseaId1en.. Kaptchuk (2003) proVides an oveniew of the issues invol,,-ed. There is some evidence 10 suggest that the soun:e of runding far cIrq studies is related to Ihe outcome. A syslCmatic ~view by l.cxc:hin el til. (2003) demonstrated a syslemalic bias in favour of the products made by Ihc company funding the rese~h. 11Ie main S1IJUIceS oflhis bias were thought to be inappropriate selc:clion or In:atmenls to compare apinst Ihe product being investiplc:d and publication bias. Porential SGUR.'lCS of investigator bias an: reviewed in detail by Oteenland (2009). Finally, publication bias (sec SYSmL\1IC REVIEWS AND META-ANALYSIS) can arise from two main soun:c:s. First. rese~hC15 arc IOCR likely to submit papc:n for publication if the n:search produces D statistically and clinically significant mAlll nIher than an iaconclusive result. Second. journal editors DR IDO~ likely to publish papers reporting SlaliSlically and clinically signiftaual JaUlas (Dubben. 20(9). lVHG
ISee also NONRESlIONSE BIAS. SELECIION BIASI A.......... P. ad OIItoa, T. (eds, 200S: EMydoptlt!tlis oj biostoluties. 2nd edition. HCM' YaIk: JaIua Wiley a: SalIS. Inc. Daft)'
_II. 0."'" Dnllllll.5. 2002: Data ~nl. bias or canfounding. BrilUIJ Medital JDllfRQ/l2S,1437-8............ B. 2009: New mdhods 10 deal with publicatian biu. BrilfM Mftiiml lOUI'M/l39. b3272. BIlla....., J. H. 19M: Selcclion bias in obscnaliaul and experimental studies. Stll'iJli~s ill Media. 13.557-67.0.......... S. 2009: Accounting far uncc:nainl)' about inYcstipiar bias: disclo-
sure is inforlnatWe. JDllmtllojEp_,Wo,y and CDnIIIIIIIrity Healt" 63,593-8. KapfdIak, T.J. 2003: E«cct ofilllcqmive biasanlaealda
cvidcncc.BriliJIIMedimII0lllflQ1l16.14S3-5.PaIta,M. .... Last,J. M. 3D: A tikI.."., of ~pitlmlio"". 51b cdilian. Oxbd: Oxford Uniwnity Pras. .......... J., ..... L A., DJaIbeID*, B. ad ad, 0. 2003: ~aI induslry spaasanhip and man:b outcome and quality: S)*mDIic .mew. BrltiJIJ &lftikalJOIII'_ 326. 1167-76. SIIcbtt, D. L 1919: Bias in analytic raeaIdL Jormrtrl ", Chronic DismsG 32. 51-63. SIlman, A. J .... MadIuIIIIIe. O. J. 2002: Epidtrniolo,iml R_S: II pr«t_ guilt. 2nd c:dilion. CamIlridF: CamIIridce Univasity Pras.
bla. In ob_rvaUonal studies In an ideal study. an invc:stiptar seeks to estimate Ihe effect of an exposure 10 a factaron an outcome ofinten:st. We mightlikc to be able to look at what happens toa population when the rac:tar is at one level and then tum back time and ~run things atlhc: second level: llul thai is impossible. of COUI'5C. Vel)' oRen it is not even possible or pnc:licalto conduct an experimenl in which Ihe levels of exposure arc controllc:cl. so that one is left with analysilll observational data Ihat occur naturally. Bias is any systematic departure from this idealised construct. which is distinct fram purely random ctTOr. which is ZCI'O on DVClBlc. The lalter can be dealt with by RlCIuc:ing variability in the measure of association. which can be 31
BIAS IN OBSERVATIONAL STUDIES _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ __
accomplished in a variety of ways. including the increase of the overall sample size. However. bias cannot be n:duc:ed by incrcasin, the sample size and it can only be conlrOllcd throup can:fully conducted research by an investiptor. 'lberc have been allCmpls to catalOJ;ue the types of bias that can occur and these broadly fall into thm: sources: the selection ofstudy subjeclS. c:rron in the information collected and coafouodin, or entangling the effeclS with other causes of the ouame (Hill and Kleinboum. 1998). In order to discuss the sources of bias in an observational SlUdy in more conc:me tenns. consider a hypothetical epidemiological study in which lhc n:su11S are summarised in a 2 x 21ab1e (showa in the table). We are inten:stcd in studying the association between expasun: and disease in a manner that avoids bias. Among the choic:c:s of study desi", from which data for this 2 )( 2 table may have arisen are a CROSSSECTIONAL STUDY. a COHORT SIlIDY or a CASKON11K1 ST1JDY. In a cross-sectional study. N subjcc:lS an: sampled and the four cell fn:qucnc:ies ddcnnincd. but in a cohort study. a groups of exposed and unexposed subjects arc chosen. essentially fixin, the lOW totals. and then the column fn:quencies arc dctcnnincd by what transpin:s durin, the course of followup. For a case-control sbidy.lhc column totals are n:prdcd as fixed and subjects dislributcd to each row within a column depending on their exposure history. which would usually be J;leaned by intervicw. Fundamental to each of these study dcsips is the ~lil8tionof a mndom sample. eilherovcrall or within lhc rows or columns. .... Ia oIIHnaUoai studies Tabu/aled resu/ls from an epitiemi%gim/ stlldy wilh Iwo lel'eiJ 0/ exposure Ilml diSftUe SilltllS
DixllSed Exposed Yes
Yes II
No
c
Total
Il+C
No
Tolal
b d b+d
Q+b
c+d N
Selection bias occurs when the propoltion rc:cnailCd from the IaJlet populDlion that is counted in a cell ofthe 2 )( 2 table depends on boIh the row and the column. One way in which this can occur in a cohort study is if there arc dilTerential diagnoses depending on the expasun: slatus. For example. SUppD5C thai an exposure of intcn:st occurs in a manufacturin, plant that proYidcs health insurance for its employees. but amon, the unexposed are substantial numbers who are unilUiuml.lfthe insured n:ceive n:,ularcheckups from lhcir physicians. this may increase lhc likelihood of a com:ct diagnosis among Ihose expased. while similar cases may have been missed for the unexposed that an: unilUiurcd.
Clearly, this would bias DD eSlimatc of the odds mUo that would be calculaled fmm such a study. Another potential soun:e of such bias in a cohort study may arise from loss to follow-up. e.g. if instead of exposure the invc:stiptor is intereslc:d in whether a person is using a particular type of In:atmenL However. suppose thai the ~tment is nul only ineffective but it also CBUSc:S unpleasant symptoms in patients who an: relalCd to the oc:cum:ac:e of the disease outc:ome. If the individuals so affeclCd drop out of the study. this would artificially lower the count in this cell of the 2 )( 2 table and bias the eSlimatc. Notice thai the m8J;nitude of the elTect of this selection bias may be substantial. even if the nmnber lost rcpn:sents a small proportion of the total. This is especially true when the proportion that develops the disease is small. so thai the portion lost in a cell of the lable is relatively high. even though the proportion lost n:pn:sents a small proportion of the o\'CI'all sample. In a case~ntrol study. a common source of bias when scIcclin, cases CDD occur when subjects with a prevalent diseuc an: enrolled into the study, some of whom may ha\'e had the disease for some time. 'Ihose who have been ill for a lon, period of time will be man: likely to be enrolled ifsuch a study design is used. a phenomenon known as I..ENGI1I-BL\S'ED SAMPIJNO. If the primary aims of the study are to study the association between exposure and the OCCUI"l"COCC of the disease, this will clearly lead to a biased estimalC of ass0ciation, but this could have been avoided by only enrollin, newly diaJ;noscd cases instead. n.c choice of appropriate controls in a casc>c:ontrol study can be an especially eammon soun:e of bias. If the cases an: scIc:ctcd from alllOllJ: those who an: di8J;noscd at a collaboratin, set of hOSpitals. then the controls should ideally be a n:praenlative sample of those \\'ho are healthy in the calc:hmcnt areas of those hospitals. If all hospitals in an an:a arc COOpendiRJ; with a study. then this could be accomplished by i1'Cl1Iitin, a mndom sample orthe overall populaJion in the geographic area. Random digit diallin, is one approach that bas been useful in populations weD covered by tclcphanes.. bu. it is bccomin, more difftcultto employ lhc method with the incn:asing use ofcum:nttcchnolOJ;ies such as cell phones. caller ID and noal lists. In some studies. controls an: scIc:ctcd ulin, subjects who have been admitted into the same hospital for a disease that is unn:laled to the exposure of intercsL This would result in a poup of subjects from the same catchment an:a as the cases. thus avoiding one SCJUI'CIC of potential selection bias. The estimate of association in such a study would be lhc dilTerence bclWccla the elTect of exposun: on the disease of interesI and ilSelTcct on the 'control disease' (Bn:s1ow. 1978. 1982). If one has chosen a control disease that is not n:latcd to exposure. i.e. the elTc:ct is zero. then the estimate of association will be an unbiased estimalC orthe effect on disease risk. However. it is often difl"u:ull to be certain thai this is the case because the assumption may just
_ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ BIAS IN OBSERVATIONAL STUDIES be the result of a lack of kaowlc:dge about the aetiology of disease affecling the conbols. A cross-sectional study can be a useful way or oblaining a snapshot of the association bc:Iwcen two or more wriablcs at a single point in time. especially if the population chosen for study is of broad interest and a carefully planned method for drawing a random sample has been put in placc.. Some national health surveys are good examples of such studies. such as those conducted by the National Cenler for Health Statistics. HowcYCl". if the aim is to study disease aetiology or other outcomes that evolve o\lCl' lime. then the single snapshot in time can be a serious limitation. For example. in an epidemiological study. subjects with a dise:ase who have been identified by a sun'ey conducted at a single poinl in time would IICC'Cssarily be a prevalent case. which is a polcntial source of bias here as it is in a case-control study. Infonnation bias in an observational study arises from cnor in the wriables that have been collected as part of the data for each subject in a study. Such cnors can either be difTcn:ntial or nondilTerenlial, i.e. random. DifTc:nmtiai error in reporting values summarised in a 2 x 2 table would arise if the cnor rate for reporting the variable in the column depended on the lOW or vice vc:n&. This would obviously be a potentially important source of bias when estimating an association. However. bias can also arise when the cnor is nondilTcn:nliai or purely random. Casc-control studies can be prone to infonnation bias because someone with a serious illness may n:member their history of exposure to the factor of interest quite differently from a healthy control. This Jltx:AI.L BIAS can be especially significant when otherstudics of the ex~ ofinlcn:st havc enlCRd the public's consciousness or been repoIted in the news. One technique for minimising its elTect is to use a wellstructured interview in which the questions havc been clearly and unambiguously phrased and posed in an identical manner to all subjects in the slUdy. This requires considerable effort on the part of an investigator. in that the questionnaire would need 10 be pre-leslCd and the inten'iewer5 weillrained. Infonnation bias can potentially also atTect a study by subconsciously inftuenc:ing evaluations by interviewers. proressional diagnosticians or eyen laboratory technicians. This could happen if the: individual has a preconceived idea of what the results of a study will be or of the way the results arc going. Thus. it is generally prefem:d that the study hypotheses not be known to those responsible for collecting the dala or that the status of a subject be masked. a procedure in which the person rec:onling the data is said to be blind with respect to the outcome. These measures should reduce the: possibility for differential errors. but nol nondilTercntial errors. While it is intuiti\'ely casy to appreciate that dilTerential cnor of measurement can bias the results of an observational study. nondiffcrential cnor can also have an effect as well. If only a single variable is affected by nondilTcn:ntiai error, Ihc:n
the effecl is generally 10 attenuate the effect. i.e. to bias the estimated association towards the null value of no association. This would tend to make the results or a study with nondilTercntial error in one of the variables c:onsen'alive in the sense: that it would make it morcdifficultlo establish that an estimated association was not due 10 chance alone. Contrariwise. il would also result in an und~imate of an effect. whK:h can be important when trying 10 delennine the public health significance of exposure 10 a particular factor. It is most desirable to minimise information bias during the design and data collection phase ofa study by minimising measurement error, but it is generally not possible to be enUrely successful in these efforts. One approach to correcting for bias at the data analysis phase is to introdUClC a correction factor that takes into account the measurement error. In the case of a 2 x 2 table. formulae ha,'e been provided for this (Barron. 1977: Copeland el al.• 1977) and similar approaches are also available for use in lOGISTIC REORESSJON (Rosner, Spiegelman and Willett. 1990). There is now a rich variety orSlatistical techniques fordeaJing with errors in variables. many of which are described in the text by Canoll. Ruppert and Stefanski (1995). Confounding arises when the estimated effect for an association of interest is entangled with another factor. pemaps one that is well known to be associated with the outcome. It is conceptually relaled to aliasing in design of experiments. in which two effects arc completely entangled. and collinearit, in other contexts. 'The potential for confounding in an observational slUdy of two variables exists when each is associated with a tbinl variable. the confounder. in the presence of the factor orintcrcsL Pn:cisc definitions of confounding go to the heart oflhe objcctives ofobserwlionai studies and various models have been proposed as a theorelical basis ror its eITect (Rubin. 1974: WlCkramarablc and Holford. 1981). Altemativdy. c:oI/apmbi/il)' is sometimes used as a simple and practical alternalive 10 more fonnal definitions of confounding (Bishop. Fienburg and Holland. 1973). An association is collapsible with respect to a putative confounder ir the estimated association is unchanged whc:a adjusUng for the confounder in the analysis. Approaches for dealing with a potential confounder are in essence to estimate the association holding the value of the confounderconstanl.ln a designed experiment. this would be accomplished by selecting strata or blocks of subjects with identical values ofthe confounder and only vary the exposure of interest within the strata. One way of accomplishing a similar elTect in an observational study is to stratify the data by abe potential confounder and then combine information across the strata. if the elTect is constant. using the MANTEL-HAENml.MElHooorsomethingsimilar(Mantcland HaentszeJ. 1959). Altcmath'ely. one can adjust ror one or IIIOI'e putative confounders by including them in a model. such as the linear logistic model (Hosmer and Lcmcshow.
41
81MODALDISTRIBUTION _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ __ 1989) or an altemaliYe CBlfltAUSfD LIIIEAR UOIB. (McCullqb and Nc:IcIu. 1989) rar D binary Iapoa5e. It is enlird), possible thDlaaobsenationalstudy will not be able to separate out the elrc:cl or an exposun: of interest froID the elrect or ziaother expos~ thai it lhouPl 10 be a aJOfounder. This is not unlike lhc more geaeral problem or eoIlinearily ahal arises in lhc context of IqI'asion anal),sis. In these silUalions. illDB)' onl), be possible to conduct a new study in which the design has been carefully conllnlcteci so that one can tcase apaJt lhc separatc contributions of a faclOr of interest from iRs confounder. TRH ........ B. A. 1917: nc eft'ectsof milclassikation on the eslimlle ofldati~risk.BiDml'triull.414_18. ~ Y.M.M., ........ S. It. aad RGIIaDd, P. W. 1973: Distnte mu/tiWll'me QllQ/yJis: tht!rNyamlpraclice. C_bridp, MA: MIT ~ss. BnIIow, N. 1978: The prupodionaI hazards madel: appIicatians in epidemioioU. Comtnlllfiarliolu in Sltltislirs - 'Th«Iry _ MlIlMRflllifI A7. 4. 315-32. BnsIcnr, N. 1912: Dcsip aad aall)'sis of auc-am1rOl 5IUdicL Annual R~rieM' of Publk Health 3, 29-54. CarnII, R. S., 1bIpptrt. Do ad SWWMli. L. A. 1995: Mmsumnml nror ill nonJiMtIT motIels. LoacIon: a.pmaa a: Hall. CopeIwd. K. T., ClltckGWaJ'.H.,M~A.J.ad RoI~R.H.I917: Bias to misclusificatioD in the estilDltiaa of n:1aIM: risk. AmeritIDI Jollnllll ofEpitkmiDIolY lOS. 488-05. HII, H. A. .... o.O.I998:Biasiaobscmlicnlstudie.s.InAmlitap.P.andCoitan, T. (cds). EIIcyt'lop«lill of biosllllmics. ~r: John W'aIe)' &: Saus.LId. B_r,D. W.... ............,S.1989:AppWloginr: regrasirHl. New VOlt: John Waley a: Sons. Inc. M...., N. ad .......*W. 1959: SlaIisticaJ aspects of the _ysis of daIa from mrospedivc studies of disease. Journal of 1M NtltiolltlJ Cllllc:er lrulilule 22, 71~. MtOa....... P. aM NeIder, J. A. 1989: GeneTaliMtiliMtD'motkIs. Loadoa: Chapnan a: Hall ROIDIr, B., SpIeaI>·n. Do . . W. . . . \V. C. 19!JO: Camctian or Ior;istic rep:ssiaa n:lalive risk estimates and canfidcnoc intcnaIs far mel-
-=
inactiWlion orllle cInag ioniazid in US adults. An accounlor the use or bimodal distributions in a mcdic.aI selling is pven in Hqberg ellli. (2001). SSE
0.20 0.15 ~
0.10 0.05
0.0 ""1....-~----,r------r--_--_ 2 4 6 8 10 Jt
bIJDadJd dlstrlbutloa Finite mixture tfulTibutitlll
.a.......,
surcmeaI enor.lbe case of multiple covariala IIICISIWd with CII'ClI'. AmerkonJDIInItIlofEpitlemiolo"U2. 734-45. JtaIIIa,D.8. 1974: Estimalinl caUSII dl'ccts of IIalmenlS in raadomixd and nonnn-
cIomized studies. JourMl tJf EtJamtioMl Psydrolo" 66, 688-701. ~ P. J. ad RaU'onI. T. R. 1987: Confouading in epidemiolopc studies: the Iidcquaf:y of the cantml paup as a IIICISIR of CCIIlf'~ Bklmelriu 43. 7SI~S.
bimodal distribution This is a PllOltABlIJIY DJS'JIUIU. with two modes. Often the two mcxa in the distribution com:spond to the data arising
TION or a FItEQlJENCY DISI'IUIU11QN
fiom two distinct populations. The nISI ligun: shows a bimodal densit)' function arising from a weipted sum or two NORMAL DlS1RI8l1rJONS (a FINITE MIXTURE DlSTRlBUIlON). An example or a histognun with two distincl modes is shown in the second ftgurc. n.c data hen: CDIIespand 10 the sw:s or
myelinated lumbosacral ventral roat libn:s laken from a kiHen of a puticular qc. The ftnI mode is associalcd with uons or gamma neurons and the second with alpha neurons. Other examples of medical bimodal diSlributions arc the age of incidence or Hodgkin's lymphoma and the speed or
fl)re size (mm x 1(t41) bimodal dlstrlbulloa Hislogrtll1l with
_be,. ddcclion Eo, mOt or G.
I~"O
distinct modes
Co, ......, F...... SuI.. J. N. (2001)
Imprvvcd evcat-relalcd fuac:tioaal MRI sipals using probability fuadiaas NeuroilnQge 14. 119l-205.
binomial distribution 11ais is the PIOIL\BD.lI'Y DISI'RI.
of the number of ·succcsses'. X. in a series or n independent trials, where the prvbability of a success is p far each llial. Spcciftcally lhc distribution is giveD by: BUOON
Pr(X = .\') = .( n~ ).,r(I-P)"-~ •.\' = 0, 1,2, .•.• n ."C. rr .\'. where n! (radorial rr) is the prodUCl or alllhc inteaen up 10 and including n and or is defined to be I. 11H: meaD or the disllibutian is rrp and its variance np( 1 - p). Some binomial dislributians with n= 10 DDd dift'cnmt values or p an: shown in the ftgun: (see PIlle 43). 11H: distribution often OCCUIS in medicine as the basis for tcsling the hypalhesis that the
_ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ BIRTH.COHORT STUDIES·
n.10.p.o.1
0.5·
0.5 ·
0.4
0.4 ·
,~ 0.2
f~0.2 ·
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I
0.0
2
0
. .\
6
8
0.0
1b
I
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.!
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Number of SUCCBSUS
I
4'6 8 Number of SUCCBSUS --'-
-'10
8•
10'
n.10.p.U
0.5 ·
0.5 ·
0.4 ·
0.4 ·
0.3 ·
'0.3 ·
1
I
J0.2 ·
Do
O.t ·
0.2 ·
O.t · I • 2
0.0
o
. 4
I
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'
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Number of succeSIBS
. 4
I
I 6
.
Number of succeSIBS
......... dlstrlballo. Binomilll _IributiolU lor mrillla mlue6 II/n lind p probability of some event of iDlCl'al IaIces a particular value. For example~ a n:sean:her ....)' poshIlaae Ihat 1041, of a populalian is iDfcctcd with a vinas and, ~n sampliDg 20 people at random flVlli.the po~~ fiDds 1h1ll6 people ha~ dae virus. Is then: any evidence dud the iDfection rate is .hi&hcr than the hypolhcsised value or 10 CJt? ~ answer Ibis .question a P-value can be computed from die biDomial distribulion as the probability Ihat 6 ·or more people in the 20 sampled have the virus wilen the probability lhat a penon is inl'ec:lecl is 0.1. i.e. Ihe sum:
~
2O! ~ 2D-. ~ x!(20-x)! (0.1) (0.9) 11M: rauiting Value is.O.Ol, givin& Sbung evid&:ace thai the infaclian rate is Iarpr Iba 10 ... As wc~ as _ling for a specific proportion. the biaomial distribution ca be usc:cl in calculatin& CONfIDENCE INT!RVALS fora pmpartion. Vallanueva ~l til (2003) usc the binomial.disbibutioa 10 c:stimale CUDftdencc: intervals ror the· pmpanion or adVerts in medical jaumals willi iDaccunde CIaiIDS. MCR clewis of the binomial distribulion can be found in AlImaD (1991). BSIiIAGL
A"-, Do o. 1991: PrtlCti~lII. "malia for nuNliclIl ~."dr. Laadoa: Chapman a HalL ~ p......... S............ J. .ad .....6, L 2003: AccuIKy of pbUmaccuticai advcdisemenls in medical jCIUIIIIIs. 14M~I 361. 27-32.
blolnfarmatlcs 'I11is is a
term given
far· the c:omiq
lOgcthc:rofmolc:Cuiar biology, C:ampulCl'se~ ~ icsandstalislics to deal with thce~-apanding genomic and prvleomic cIaIabascs. which are themselves Ihe result of rapid lcchnoiogiealMlYllllC;cs in DNA sequencilll, gene e.xpJaSiaa measuremc:at and macromolc:c:ular strudun: dc:acnnilllltion. In many cases sue" techniques pve rise 10 HIGH DJr.tI!NUDNAL DATA. A coJl1lfthensivc accounl ofbioinforrnatics is giw:n in Zvclebil and 8aum (2007). BSE ZYIIIIIIL M.. .ad ......, J. 2007: Ulltkrsllllllli", biDitlftJrmtllil:~
GIrIaad Scieace.
birth cohort studies
'I1x:sc IR stuclieseSlDblishecilo
e.xamine grawth. development and health or cbilcln:n flUID binh. ~~ giftn sufticienl follow-up they also provide 43·
BIRTH COHORT STUDIES _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ __
insights inlo inftuences on aduk disease that operate throughout the life coune. In principle. a birth cohort study is one in which all study participants are recruiled al birth and then followed over lime. The cohort is defined by the localion and the lime period in which the participants were born, which may be those born in one week or over a period of a year of more. The members of the cohort are then followed up at various lime points to ascertain risk factors and health outcomes. As the cohort ",es the focus of the research lends to shift. In the early years. the emphasis tends 10 be on childhood poWlh and developmenl and risk of childhood illness. but as the QObort matures adult risk factors such as smoki", and obesity and health measures such as blood pressure stan to be of greatel' interest. Oulcome variables in childhood such as height can laler be conside~ as risk facton when assessing chronic: disease later in life. Inlergenc:ndional and genetic faclOrs are of interest and infonnation on family members is included in many birth cohorts (Lawlor. Andersen and Baity. 20(9). The first cohort to be established using recruitment at birth was the National Survey of Health and Development. which slUdied babies born in Britain in the fint week of March 1946 (Wadsworth el at•• 20(6). The eohort has been followed up on more than 20 occasions since birth. the latest being at age ~ years. Contacts with the participants ha\'C been by postal questionnaire. home and cliDic: visits. and through schools and links with health and educational professionals. Brilain has lwo oaher birth cohort studies conducted on similar lines. They comprise those born between ahe 3 and 9 March 1958 (Power and Elliott. 1992) aad between 5 and II ApriI1970(EliiollaadShepbenl.2006)respectively.Both studies have included a number of follow-ups that have gi\'en insights inlO the powth and development of these cohorts through childhood. adolesc:ence and into adulthood. Crosscohort comparisons have also been possible and have allowed examination of secular tn:nds. e.g. inlO Crohn's disease. ulceralive colilis and irritable bowel syndrome (Eblin el at., 20(3). The Millennium Cohort was recruited in a dilTen:nt way (Smith and Joshi. 20(2). and a further cohort study is planned for births in 2012. Birth cohort slUdies are not of course confined to Britain. though until recently comprehensive national cow:rage has ruely been allemptcd elsc:where. The Scandinavian counbies have well.developed lin~e systems and in Norway and Denmark studies or ovel' 100 000 births have been launched (Olsen el al.• 2001: Magnus el al.• 2(06). and the United Stales has embaJted on a study of a similar scale (Branum el at•• 2003. and sc:e hllp:l/www.nalionalchildrenssaudy.gOY). Frequently. birth cohorts an: located in one town or city. For example, the PeIOlas Birth Cohort Study in Brazil n:cruiled all births born in the cily of Pelotas during 1982. It represents a good example of a birth cohort study with
long-term follow-up in a developing country (Vic:tora and Banos. 2(06). Many birth cohorts have been defined retrospectivcly. Thus births in a defined geographical area during a specified time period ~ identified from established records. The dala can then be linked to other standard records such as death indices. or the sludy population can be traced and those slm alive can be assessed by post or by interview. An example of this is the birth records of the 1920s and 1930s from the English county of Hertfordshire that were extracled in the 1980s. The population was lnIced through the National Health Service Cennl Register and details of deaths and current general praclitioner addresses obtained. This allowed nol only an analysiS of mortality in relation to birth and infant weighl but also enabled follow-up of the survivors to examine them for risk factors for chronic conditions s~h as cardiovascular disease (Syddall el at•• 2(05). Some retrospectively defined birth cohorts have focused on particular events that gave rise 10 extreme liying conditions. Forexample. those born in Amsterdam in 1~1945 around the lime of the famiRC imposed by the Oennan occupation have been followed up 10 assess the impact of famine at key stages of pregnancy and early life (Roseboom el at.• 20(1). Similarly. a cohort of men born in 191~1935 WCI"C identified from one district in Leningrad. a third of whom had experienced starvalion during the siqe of Leningrad in 1941-1944 when the)' were around lhe age of puberty (Span:n el al., 2003). The whole cohon was followed up and invited to take part in health examinations to assess the long-Ierm effects of the famine. There is also inten:st in defining birth cohorts at an earliu time point than birth. A child's growth and de\'Clopment begins before birth and so characterisalion of aspects of pregnancy is considen:d importanl in determining the long-term in8uences on the olTspring's health. The Avon Longitudinal Study of Parents and Children (ALSPAC) recruited 14 000 pn:gnant women resident in the English county of Avon whose expected dates of delivery wen: between 1 April 1991 and 31 December 1992. The women and their offspring have been followed up by means of postal questionnaires on many occasions and a subsample known as the Children in focus was seen at clinics 10 times before abe age of seven )'C8IS. From that age onwanls clinics bepn for the entire cohort (Golding el at•• 2001). lhking this one step further. with an increasing focus on the very early origins of life. two cohort saudies have recruited women hefon: pn:gnanc:y. The first of these recruited some 2500 women in six villages near Pane in India. Of these. OYU 1000 became pregnant and full data were obIained on nearly 800 births. This c:ohoIt has now been followed up inlo adoleseence (Rao el at.• 200 I). In the UK. the Southampton Women's Survey rc:auited over 12 SOD women aged 20 to
_ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ BIVARIATE 8OXPLOT
34 years when they wen: not plqlUlDt aad over 3000 orlhcm we~ studied throlllhout subsequcat p~pancies and Ihc chilcm,n are being rollowed up (lnskip el QI.~ 2006). The ~cal1y launched US Nalio.... Children's Study is mainly ~ruiting women ill Ihc first trimester or pn:gnllllC)' but is also including some women beron: conception (hUp:l1www
.nationalchildn:nsslUdy.gov). Birth cohort slUdies ha'VC many Sln:nglhs. Usually they
aaptuR: a mJIiSoSICCtion orlhe papuIaIian and lhey havc all die adWDlllpS orlongitudinal studies. However.1he weakness is tlud over the lire counc a lugc pen:entqe or prospectiyely defined bilthcabans lends todRJp out. MIlD)' DIIOFOUTSan: due todc:alh as thccohort ages or to mipation out orlhc "'lion or c:ounlryof study. Persistent questioning and n:qucsls to attend clinics 01' be Yisitc:d at home adds to the albition. as IOII1C participants fccl ....t they baYC conlributcd CROUgh and lheir motiVlllion wanes. Tbe ~maining cohort may no 10000r ~nt Ihe general population. Rc:IraspecIi'VCly defined cohorts CaD suITer less flUID this problem but then they oRm lack suflicicnl dala on die early ycars. HI (See also COIKIn' snJDIfS)
BnIIImI, A. M.. Co'awn, G. W., eon.. A.dal. 2003: NIlianaI Childraa's Study or envinwnental effects on child health and cbdopmcat. En,inHrnren'a' Hm/," hrJ/WcI;re 111.642-6. DdIII, A. G. c., l\~, S. M .. EIdIom, A., .......r, .. Eo &lid Wak...... A.J.2OOJ: PIe\'llleaceof lasaoinlaliaaldiscases in two British Dati'" binb cabons. Gu, 52. 1117-21. Ill", J. ad Sllepllenl, P. 2006: Cohort pmftic: 1970 British Birth CaIat (BCS'70).IRlmIII,iDlltll JoumtI' ofEpitlemiolol>' 35. 836-43. Goldm.,J.,........,.. M.,J--. R. ........ ALSPAC...., T_ 2001: AUPAe - The Avon LonPtudinai SIUdy or Pumts and Childraa I. Sludy methadoiCICY. PtIe_'r;~ tnttl pm-'ol Epidem;' oIogy 15. 74-87."",. H. Mot GadI'n)', K. M., ItDIIIDIDa, S. M.,
11Ic Millenniwn Cahart Study. Pop,,1or Trmtb 107, 3Q..4. Spuft.
".1IDIbJ.,
POI Vipri, 0., SbesIoY, 0. 8., s.. Puf'IIImI, N.. ......... V., PaIaroI, D.... 0aIaIdI, 1\oL R. 2004: LaIg tena mortality after sa~ SW'VIIion dun.. the liege of Leninpad: pnlSpCCtivc cahan ady. B,'tUII lIedital JDllrIftlI January. 321. II. 17........ R. Eo, .\ale Sa)w. A., ........., & M.. Maa1ID, H. J........... D.J. p.. C'Gaper. c. ........ ReItfDnllbln CoIIarI StadJ GnqI200S: Cohort pmfiIe: 11aellcdfonlshiR Cohort Sludy. In'mNlliontII Journal ojEpitienriology 34. 1234-42. Vkton, C. G. "'1IarnI, F. C.2006: Cohort profile: n.e 1982 PcIotas (Bruit) Birth Cohad Study. In'~nrtI'ionaJ JOIII'IIIII 01 Epitkn,iDID,J' 35. 23742. Wadswartll, 1\0'" XIIIIt Do, au.:..rds, M. R. 2006: Caban pralle: The 1946 NIIIionaI Birth Cohort (MRC N.a.aI Survey of Heal... and De\'Clapmeal).'If'e1I1t1,itNrtllJOUI'MI 01 Epidemiology 35. 49-54.
"'1IanI)'.
blserla' correlation
bivariate boxplot 'l1Iis is a two-dimensional analogue of the BOXPLOI' for univariate data. which is based on calcuIDling "rabust~ measu~s or locatioa. scale and com:laliOD. It
or
consists essentially a pair of conccalric ellipses. one or which (the "hiIllC') includes 50'1, the data and the other
com:laiions and large rorsmaU absolute values. Dclailsorlhe construction or the biyariak: boxplot an: p'VCn in GoldberJ and Iglewicz (1992). This Iypc orboxplot may be useful in
nee 0
~r" -:::r.::.. \ /. }.,
..... K., N,ad, W.,SkjMn... R. ................ C. 2006:
Study). Intmlll'iontIl JDllrlltliol EII_mlo." 35, 34-41. .... Sa, y~ c. s., K....... A....... C. H. D.. Maraetll, 80M., J. . . .A.A..SIder. R.,JGIIII,s., Rep.S.. Lubne, H. ... DIal, B. 2001: ..... ormicranutricnt-rich foods in India IIICIIbcn is associated willi die size or lbeir babies • birth: Puc Matanai Nutrition Study. JDUmG/ol Nutr/,1oIr 131. 1217-24. ItaIIbooIII, T. J.. tall . . . Metdta, J. H. p.. 0IIaaad. c., Barbr, 0. J. P., . ., ...... A. C. J. ad Blebr, o. P. 2001: Adult survival after expGiSUlIC 10 the Dutch famine 1~5. Pardia'ric ontl P«ind,a1 EpitlmJiology IS. 220-5........ Ie. and J.... H. 2002:
on
prcu'"
or
(called Ihe "fenan which dclineales potential wubJcsomc outliers. In addition. raiSlaat ~I~ssion lines of both y an x aad .'l on y 1ft shown, with Ihcir intersection showilll Ihe biYariatc locations estimator. The aaatc angle bc:awecn Ihe ICgn:ssion lines will be small for a IIIIIC absolute value of
.....,C.M.,Barbr,D.J.... CaapIr.C.2006:Cabortpmft1e:11ae Southampton Women's Sunoey. hrlmllll;olltll JDUmGI t1/ Epidemiology 90. 42~. Lawlor, D. A., AIIdeneII. A.l\L I11III Batty, G. D. 2009: Birth c:dtart studies: put. Pft:SCIII and fUhR-ln'l!I1ItIliolllll Joumol of Epitlmriolo".18, 897-002. Map..., P., ..... L M., Cahart pmft1e: The Narwqian MadIer and Child Cohort Study (MoBa).IIf,nnoliDlltllJOIITIItIlojEpiden,ioIolJ' 35, 1146-50. 0Isa, J., l\felbye. M., 0 ..... S. F. ~ III. 2001: The Danish Natianal Binh Cahart - its backpound. strucI1IK IDII aim. SmntlintniDn JOW'IIa' 01 Pubik Hm/'Ir 29. ~7. Penr, c. ... EllIott, J. 2006: CGbart profile: 1958 British Binh Cohort (N1IiDnaI Child newlopnnt
Sec CORRELAnON
,
/
,
I· • I
\ __i • DeInIII .. I ,
I·I
.0,J
\
I
I
\1~/ o
500 1000 1500 2CIOO 2500 SOOO Number of manufaclurlng enterprises _oying 20 or more workers
blYlll'late IIoxplot SCQ',erplol 0/ sulJur dioJci_ concml,Q-
lion QlllinJI nunrber D/nJIIIIlI/tICluring mterprises/or citws ;n lire USA, mowing lire bivtll'itlle boxp/o' of ,Ire
.'Q
4&
BIVARIATE DISTRIBUTION _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ __
indicaling the distribulional propc:rIies of the cIaIa and in idcntifyinJ possible outliers. An exlUllplc faraSCA11ERFI.DTor the number or manuracturing enterprises cmployina mo~ than 20 people: qainll the: polluti_ level as measured by sulfUr dioxide c:oncc:nlnllioa for a number or us cities is shown in the ftgun: (sec JNIIC 4S)~ fiYC cities ~ indicated as outlic:n. rour thai haw: man: than a thousand manuracturing cnIcIprisc:s. bul one. Pnn'idencc. thai has only a n:laliYCly small number or manufacturing cnlClpriscs. SSE (Sec also SCA111!IlPI.Dr MATRICES) GaIdbera, It. M. ad JaIewkz. B. 1992: BiYariate extcnsialls oldie
boxpkM. TuluIDnretrit$l4. 307-20.
bIv. .ate distribution
For each and evcl)' pair or reasible values. lhc probability thai a pair or variables will lake IhaIc values. 111is lhcn is a naIUral exfcnsion of the idea of a lDIiYariate prababilily distribution. applicable when we ~ measurinllWo paiml Yariables.e-l. a penon's height and weight. If Ihe two variables ~ independent then tile bivariate clistribulion will not be of puticaIar inten:&L When they ~ CXIIIelated. as willa height and wcilht. however. it becomes importanl toeansiclcr ahc bivariate cliSlribution.lrwc wc~ to look aa a sample we might scelhal20" orlhc sample an: over 6 reet tall and 20., of ahc sample ~ under SOq in weight. but only by IoakiaI aa Ihc bivariate dislribution would we know ahat Ihcn: wen: no (or rew) peoplc who wen: bath over 6 fi:ct IaII and under SO kg in wei,ht. When:as univariate distributions can usually be depicted in a BAR CHART or 1IIS'I'OOItA1I, bivariate distributions. clue to their additional dimeDSion. cannat. Ir Ihe two wriablcs ~ categorical then a simple crass-tabulation will pmbably be most informative. while irthe two variables an: continuous a SC'ATI'fllPlDl' will probably be apprapriatc. Par eumple. whaals in pnMOUS univarialc work Mcl..arc:a ellli. (2000) hayC sepanllely lookc:cl 81 the distributions or n:d blood cell volume and hDClDOllobin levels when idcntif'yina anaemia. in a mon: sophisticaled approach, Mcl..arc:a et III. (2001) cmploy a biyariatc distribution or n:d cell volume and haemoglobin. The masl commonly cncou~d bivariate distribution is the BIVARIATE NOR1W. DISTRIBU11OM. a special case or ahc MUIl'IVARIATE HOB1AL DImUBUIlON.
AGL
Me...... C. It., "am......., &. L, Mc~ O. J., """'111, II. C.. U, G. M. ad .1d.aND, G. D. 2000: PIIient-spcc:ific ....Iysis of sequential hIcmatoIopcai data by natliple Unear ~ and JIIimR disarillulion moddUnc. Sttlti.rtiu in Mf!tiicillr 19. 1,83-98••1d.anD. c. E., c.Ia. LV.. s.,tII, p.
x.. ...........
_ Md.""•• O.J. 2001 :CIassific:lIIioaofcIisordcrsofancmiaon the basis of millhDe . . .1 paIBIDdCIS. ndnical Report 01-56. Iniae: Infonaalion IIIId Computer Science Department. UaiYCnity or CalifomiL
bivariate normal dlstrtbutlon Tbisis a special case or ahc multiwriatc nonnaI distribution with two variables and the IIIII5l mmmon example or a bivarialc distribution. The bivariate normal dislribution is worthy of mention because or anlhe multivariate nonna) distributions it is Ihc IIIII5l conunonIy usc:cI.1he casielllO i1luslnfc and lhe easic:sl to write out in mathematical natation. Oiycn two variables, X and Y, the probability density function of the biwrialc normal distribution is defined by the mc:ansof X and r(hen: dcnolcdllJt andllyrapecliwly). lhc STANDARD DEYIA'I'IONS or X and Y (hc~ dcnolcd tlJt and tlr n:spceti\ICJy) and lhc CORRELATION or X and r (dcnaled pl. Given lhc:se values, the pmbability thai X and Y bike values x and y n:spcclively.J(x~). is: 1
1
1 [ (x-IiX) I(x.,) = exp Sf 2."l.tIf,;r=p'l 2( I-p-) til. {
This ronnula may not appear particularly plc:asana. bul is easier'1O hancIIe than for hillier variate narmaI distributions bcaause of the siftJlc c:orn:lation involWICI.. For runhercldails of the dislributi_ sec OIalficld and Collins (1980) and Orinuneu and Slirzaker (1992). When paphed as a SC'A11EIPI.Of, data rlVm this distributian will appear as a cluster or points in an approximately elliptical shape willa the density of the points being gn:atcst. allhecen~ of the ellipse. 11Ie location of the ellipse will be dependent on the two means. while the standard deviations and correlation dclcnnine the angle and spn:ad of the ellipse. The ellipse gels 'narrower' as ahc mqnilade of tile c~lation increases and approaches a slnIighllinc al p =1 or -I. Suryapnmata et til. (2001) use the bivariate normal dislribulioa in onIcr to compan: simultaneously the clinical effcctivcness and cost-cfl'ecliyeftCSs ortwo lrealmcnls ror patienls willa acute myocardial infllKtion. By dnwing a graph of the difference in el1'ecl q.insl the diffen:nce in cosl they W~ able 10 illustrate a CONFIDENCE INTERVAL ror the clilJen:nces between the two tn:allllCnlS as an ellipse. A conYenienl property of the biVariate normal clislribution is ahc ract thaa the IDIII'ginai cliSlributions oflhc two wriables an: uni\rarialc narmaI: i.c. ir Yis ignon:d.lhcn Xby itself has a NOBW. DISTRIBU1'IC»f (and vice ycrsa). Also. the condiliaaal disbibulicms or X and Y are nonnal. To put dais another way, if Y is observed to take a particular yalue. dacn dac
_______________________________________________________________
unknown value of X saill has a nonnaI distribution given this knowledge. AGL
CMaIIId. C. aDd C....... A. J. 1980: Introt/lleUon 10 nadlia'tlritJle DIftlIyJiS. London: Chapman & Hall. GrImmett, G. R. .... stInaker, D. R. 1992: PrDlxlbility and rmrJom prtJeGJD, 2nd edition.. Oxford: CIIIKndOll ~ss. 5111')'.......... H., OUenanaer. J. P., NIhIIe...... Eo, , ...'t Har. A. \V. J., HooraUe, J. C. A., de Beer, M.J.,AI,M.J.aadZIJI...... F.200I:Long«rmoutcomeudoo.steffectiYeDCSS of stenti", ~rsus balloon angioplasty for acuIc my~
canlial infarction. NeDrl IS, 667-71.
Bland-ARman plot blinding
See UMIlS Of A(Jlf.BtENf
Sec CUNlCAL 11UALS. CAI11CAL APRAISAI.
blocked randomisation
Sec
RANJX))dJS,o\TION
Bonferronl correction This conection is used when pcrfcxmi~
multiple signiftcance tests in order to avoid an excess of false positives (ScbaJTcr. 1995). Suppose. for example. S'nJDENrs is to be applied to sample data on six variables to assess mean diffcn:aces in two populations of interest. If lhc NUlL HYPOJIIESIS of no diffe~nce in means holds forcach oflhe six wriables. and each of the six lcSIs is perfonncd at lhc 5 CJt SICJNlFlCANa L.EVEL. lhc probability of falsely ~jc:ctinr; the equality of at least one pair of means is 0.26 (this assumes the variables are independent). a ftvefold increase o\'er the nominal significance level. 11Ic Bonfemmi c:om:ction approach 10 this problem involves using a significance level of ~n rather than ac for each of lhc n lesls to be pcrfonncd. For a small number of multiple tests (up 10 about 5) this method proVides a simple and acceptable answer lo the problem of inftaling the 'JYpc ) error. The correction is. however. hiply conservative and not recommended if large. numbc:n of lests are to be applied. panicularly sinee its usc can lead to the rather UDSaIisfactory situation where many tests are significant 81 the « level but none al level rUn (Pemeger. 1998). In addition. lhc 8onferroni concction ign~ the dcgft'C to which the wriables may be CDlKlated. which again leads lo coRSCl'\'8tism when such ~lalions ~ substantial. SSE ISee also WLTIPLE COMPARISON PROCEOORESJ
'-TEST
........r. T. V. 1991: What's wrong with BOIIfenani aGj1IStments? BritimMtdicalJ0III'IftIl316, 1236-8. SdIaII'er.J. P.I99S: Multiple hypodlcsis tali",. Annual Rra'ieM' of I'S)v:hology 46, 561-84.
boosting This is a class of optimization algorithms that can be applied to lit a number of classical and modem statistical models. Its origins come from machine learning and aJIIIPUICr science (Meir and Rilsc:h. 2003: Schapire. 2003) but have been adopted in statistics as well. From a statistical point of view. boosling works by iteratively fttting
~STRAP
residuals obtained from rather Simple reg~ssion models (BOhlmann and Holhom. 20(7) (sec MULTIPLE LINEAR REDRESSION). These models ~ called base-learners and determine the structure of the linal model which. in esseac:e. is the sum of all base-Ieamers. The method is altraclive because it can be applied to multiple linear regression. LOOJS1lC REORESSlO.... classiftc81ion. SURVIVAL ANALYSIS. robust regression (see ROBUSTNESS). QUAJII11LE REDRESSION. etc. Furthennore. the rq:ression relationship can be ~stricted 10 linear or addilive funclions. which facilitales interpretation of the ftnal model. Unlike RANDOM RHlESTS, boosting is sensitive to the most important hyperparameter. the number of iterations of the algorithms. Too large values will cause overfilting. Thus. crossvalidation techniques have to be applied to detennine an appropriate number of ileralions. The algorithm is especially useful for model filling for HIGH-DIMENSIONAL D.O\TA. i.e. when the number of observations is smaller than the number of elplOl1ltory variables. Models filled by boosting algorithms have been successfully applied to weight estimalion for foelases by three-dimensional ultrasound imaging or for predicting cancer subtypes based on gene expression and single nucleotide poIymorphisms (SNPs) dala. TH
an......... P. ad HatIMn, T. 2007: Boosti", algoritJu.: R:pluizalion, pmlictioo and model filling. SIDtulicai Sdtrlce. 22(4). 477-505. MeIr,R.and Ri.... O. 2003: An iatnxluction to boosting amd Icveraciag. In Am'tllftm lecillTe3 Off nltldJiIre l«U'ning (LNM2600J. Sc••ptn, R. E. 2003: The boostinl applUllCb 10 machine lew",: an overview. In Denison. D. D., Hansen. M. H..
Holmes. C•• Mallick. B. and Yu. B. (cds). Nonlilreor ellimlltion and cltmijitDtion. Ne\\' York: Springer.
bootstrap The bootstrap is a computationally intensive technique for slatistical inference. which can be used when the assumptions that underpin much of classical statistical infen:acc an: questionable. Tbis may be because the data are not nonnaUy distributed or the dataset is small so that thccRtical !aulas based on larJe sample theory are inapplicable. For elample. the bootslnJp can be used to estimate the BIAS and STANDARD ERROR ofparameterestimatcs togethcrwith CONfIDENCE ImERYALS.
)n effect. as we illustrate in the figure. the boocslrap is a data resampling technique. It was ronnally introduaxl by Efron (see the discussion in Efron and nbshirani, 1993) aDd. although it has a sound thean:tical basis. the idea the~ is something magical aboul it is rcftectcd in its name. The tcnn boolSlnlp derives from the phrase to oncselfup by one's boolSlnlp. widely thought lo be based on one of the 18th c:entwy &dvenllRS of Bamn Munchauscn. 111e Baron found himself at the bottom of a deep lake and saved himself by hauling himself up by his bootstraps.
pun
47
BOOfSfRAP _________________________________________________________________
'. . . ..... '. . .. ... .. "' ............ ·.1 . '. . .. . S: ".': .: ... Ie ... I••: • • .. •.• ·.a •..•• ':: •.••••.••..•••• : •.•.• ,..: •..•••••. 2: .• ·.·: .. ' . .... .. ..... ......... ......... ..... ' . ..'" .... ..... " .. ,
• 7.: ... •••• • 12 • : t : .. ' : .... : :...... • ..'
'. •
•
.. " .... .. • . ' .. '... ..": • ... 10 ~. : .: ..
. . . . . .. .. • ....... •• ...-. t t • ~'...... .~." ~"
It'
9 ......1
....
.. .... : . I I ·
~
Population
parameter value •
...
'I 10 '11
Sample
2 12 4 7 I
parameter estimate 6
'5 986
S 2 15 I
., 6
8 2 'I 'It 7 2
to
2 4
241'1 '12 7 I f 7 '11
8 6 2 t '1284 8 4 'I 8
.,
7 '12 4
2 S .,
'It " 7 • 'It'lO 16.
I '10 15 .8 I 10 2 1
S 9
28 84 'It 912 1 o t
2 1 2 5
,7 4 '12 2 • • 1'112
7 Bootstrap samples
parameter eslimales 141 ,",0s,04,OI_"~ 6
•
'.
•
•
'6
•
boatstnIp S~he",a'k Illrut,lllion of boDt,t,apping We will describe the idea using the figure. Suppose we ha~ a population in which the true value of a quantity of intaat. say adult height. is c1cnOlc:d by O. We wish to estimate (J and take a sample or 12 individuals &am dUs popuIalion. In die fllIR- Ihe populatiaa is dcaoted by the IBlle m:1aDJIe in the first row (note that the numbc:n idenlify ~alaljon mem~ a I R not their adult heights). In this population.. the 12 individuals to be iDcIucIc:d in the sample an: numbered. They comprise the actual sample, which is shown in the sccond row. Our estimlllC or adult heiP~ calculalc:d &om this sample. is dcaaccd by 8. In order to quanlify how close 9, the estimate of adult heipa in aur sample, is likely to be t06, the actual adult height in the population. we need althe very least ID c:stimaIc Ihe variance or8. Imqine doin& Ibis in the followin& way. Take a lqe number, say B. of samples of size 12 from the population.ln each of these samples. calculate an estimate ofadult heiJht. Call these e:stimates 8" ... ,0,. Then estimate the variance of 9 by the sample variance of (9...... 8,). Of CIOUI'SC, dais appmach is impossible in practice; if we could doni to draw B extra samples of size 12. we waald ha~ dnwn a much larger sample initially! However. an appro.x.imation to it can be achievc:cl as follows. Suppose we sample with n:piaoemcnls from die 12 absenatiolW in the data (second lOW in the figlR) to fonn a ~subsample'. also of size 12. Seven possible such "subsampies' an: shown in the thinl row onhe IigIU'C.. Forcxample. the ftr.st subsample. shown in Ihe lint IeClanIle in the third IUW. eonsists of the follOWing observations (note some ~a lions will occur II1CJm than once, and some not at aD): C1.2. 2. 2. 3. 3. S, 6. 7. 7. 8. III. These ·subsamples' 1ft known as boot,t,ap somple,. Using each of these bootstrap samples we calculate an eslimlllC or adult height. By conll:nlion. these ~ denoted with a •••• to indicllle lhey have bc:ea calculated from a bootslrap sample. From the seven bootstrapAIBmP~ in the thinl row or the figure. we therefore gel 6" .•• ,87• Now
we simply estimate the variability or the estimate or adult height calcuJaaed from the aclllal +ta. py the sample variance or the bootstrap estimates 9., ... ,0,. or course. in praclice we waald need many IlIOn: than seven bootstrap eslimales. Another way of IookiDg at this is as follows. We wish to 1e:8111 about the mationship between the lruc population panuneICr value. 9, and c:sIimates of(J obtained &am samples from the population, denoted To do dais, we pn:tcncIthe observed cia.. an: the populalion and repeatedly sample from the dala to lcam about the relationship between iJ and c:stimatc:s abmined tiom the n:sampled d_ dcaotcd In other words, we say:
6,
9.
o... .
Di,lri""IiDII of eslimtlles 9gimr6 is lIPP,oximtlteri by
(I)
DistributiDn of e,timate, if giren 9 This is known as the boout,tlp principle. It is impartanl to separate this principle from simulation.. which is used to eslimatc the distribution ofestimates 6 given 8. In fact, then: IR two potential IOUrces or error in bootstrap procecIun:s. The first arises because the boocstrap principle cIac:s not hold lnIe, i.e. the two distributions in equation (I) an: not equal. The second arises because we only usc a finite number of baotslrap samples. B,ID eslimllle the distribution of the , s. However. this error can be made as small as we like by simply increasing B. whe:reas the: boaIstrap cnor is lied. One: of the ans or bootstrapping is to mnsiclc:r simple functions of 11. such as (9-9)/11 (when: II is the sample stanclarcl mor of 9), for whioh the bootstrap principle is more nearly bUe. 10 make things mon: concrete. we ilIUSlrate how to use the baotslrap toeslimlllC VAJUANCE. Considuthe data in the table.. We an: intcn:sted in estimating the a\'Cr. chanGe in the carbon IIIDDOXicIe transfe:,. fador. The obVious estimate is the mean: (33+2+24+27+4+ 1-6)11= 12.14. Suppose ...
A
_____________________________________________________________ 'we wae ~Ie 10 draw a lar&e a~.1J, samplesoflhc: ~ size u ..., in Ihc: table fmm the 'popIdaaioa' of ~
with ellielcenpox and c:atillllde Ihc: a\Wllp chinle aD .c:acb. Denob: Ihe n:suIlilll cstimala by 91 ••• ~ , ii, and recalllhat the InIevalueiD thcpapulalian iscalled 9..Thca an esIimalc or the varimJec: would be:
IIIOIIDXftIe,,.,,,,.
.......... 011111"" II. ctrion ./tld",..for dtklcapo.Y. ",..,mI. tJdnrbSitm," 1larpi11ll1lRlltI/kr tI sillY of11M ..wi (Din." I11III Hilrlcky.
.... ""6 wiI. 1997. p.6l1
En,,.,·
Wark
C""",e III (Wft'k - Enlry,
1 2 3 4
40 ·50
73 ·52
33
5
60 62
PtI'''''
6 7
56
80
58
15
66
64
63 60
hquenc:y of Ihese ot.r¥aIiaas in abe data in die ftatlable;
"y ·aII accui' GIKle. Rows ~Il show Ihe fn:quency or IIae observations in boatstrap umplc:s l...g.
Thus.
ia the 8nl
baolIInIp cia'........ obsc:naIian 1~s DOl appcaI',obscn.aIion 2 appealS ~ ~ absc:nali_ 3'~ twice.. Dbaer..; vati_ 4 once. obIerYaliDa 5 cIocs DDt appear. observalian 6 appealS ancc and oIa:rwitian 7 does DOl appem-: lite IIIC8D is dlen I!.71. ~ table shOws B.9 baolIInIp S8IIIpIcs. We Ihus have 9.1, •••• each..of ~ch . . . . ill approxilnab:ly Ihe &1liiie ~llIlicmIIIip to 9 u 0 does 10 the IIUe parameIer 9. We can use"'" 10 learn about Ihc ~laticiaslUp ___ ; aad O. $Peciftcally. the baolIInIp nlillUde of variance is: . . .
0,.
1 -B
2 24 'Z1 4 1
~NP
te"...~2 r-I
0.·-6 r
(3)
CcImpIIriIll with (2). we see the baolIInIp vasiaa (3) is _hal by (a).pUltiIll "'. na~ 1D~iD& with a ·hat". and (b) puUilll a ..... Oft wbaI is left. 1his rule oflbumb is ftI)' UBCfuI in practice. SubslibltiD& Ihe baolIInIp cstiIIIab:s Iian die secand IIIWe
-6
gives:
• (9;-9)1 -I~.
(2)
B,:
~ [(11.7.-12.14)2 + (7.00-12.14)2 + (18.57-12.14)2
UsiD& Ihe boubti. principle: (I), we CSIimu this by (a) . . - . 9 by its p.ae &am the _ 0, aacI (b) . . - . dac: iii by. ii. wlacn: cac:h is the IIICIIIl cadIon monoxide . . . . . in the ilh bootstrap sample.. The secancI .... shows the boaIslrap in action. 1'hI: ftnI lOW shows lite absenrccI diff'cn:aces, conapondilac to the rourdI co"ma of . . Intlable. ~ IKCIIId nM shows.the
i;
+ (1,.43-12.14)2 + (15.71-12.14r + (26.43-12.14)2
+ (13.29-12.14)2 +(24:29-12.14)2 + (16.43-12.14)1]
= 7.112
.........pFnqwnriawil. ""'klr.m~fnJm '.tWiginlll.'lIm 'kjin' '''''tlpJlNrlnern:'' t1f"_~'rk bDoI.,,.. ..",.. SItI'Ulk
0bIcI val differences
Flaauenc:y in
33 1
observed clara lit bootllnlp sample
2 1
24 1
27 1
3
2
1
1
2ad bacIISInp I8111pIc
1
I
.3n1 baotsInp IIIIIIPIc
3
I
4dI boaIstnIp umple
I
I
SIll boaIstnIp IIIIIIple
7.
4 1
1 1 1 1
1
2
1
2
1
2
2
2
6Ih boaIstnIp IIIIIIple
4
1
1
1
boaIstnIp IIIIIIple
I
2
1
1
8th boaIstnIp umple
2·
I
2
2
9dI boaIstnIp IIIIIIple
I
1
1
2
-6 I
I
I
1 2
2
(me_)
..
B= 12.14
'I...... =
11.11
... = 18.51 ... ' .. = 15.43 ... "... = 15.11 " ='26..43 ... IJ., = 13.29 .... '.... =24.29 " = 16.43 '2 =7.00
0]
I
41
BOXPlOT _____________________________________________________________________ However. B = 9 is nOi nearly enough. 'l)pically we may need BIOWld B 800 boatsb'ap samples lO eslimate the variance accuntely (Booth and Sarkar, 1998). Taking B= 1000. we ftnd lhatthe bootstrap variance of the mean is 5.392• which compan:s with the maximum likelihood estimate of 5.382 • 1be bootstrap eslimlllC of the standard enol" of the mean. 12.14. is thus 5.39. Of course., this example is only illusbative; we know the answer anyway. Howeyer. in many circumllanc:es we may not. e.g. if the data are nOl normally distributed and we want the slandanl enor of the median or some Olhc:r nonslandani measure of the data's 'cenlle·. The bootslrapprinc:iple can clearly be applied much more Widely. It is prvbably most often used to calculate confidence inlc:rvals (Carpenter and Bithell. 2000). where it avoids the need to n:ly on large sample lhc:ory or assumptiOM coneeming the dislribulion of the data. For example. the distribution of individual patients' hospital costs is usually very skew and the bootstrap has been applied to calculate conftde:nc:e intervals for the average cost of hospitalisation. Other applications include hypothesis tesls. power calculalions and estimating the prcdicti\'e performance a slatislical model will have when applied to a new dataset that was not used in fonnulating or estimaling the model. In order for the bootsbap principle (I) to hold, it is necessary fOl' the bootstrap sampling 10 mimic the actual data sampling. l'ben:fon:. if we an: bootstrapping a c:linical trial with twolleabnents. we should sample with n:placement within each tn:atmenl paup. to preserve the nmdomisalion. Other situalioM requin: diffen:nt approaches. The booIsbap resampling illustrated hen: does not depend on any statistical model and is an example of the no-ptlrtlmelric boolstrDp. An altemali\lC, the paramc:lric bootstrap. is less widely used. This samples data from a parametric slalistical model, such as a n:;n:ssion model. nuhc:r than wilh n:platlemenl from the observed data. Lastly. nOle that the bootstrap. although it uses simulation. is cbarac:terised by the boolsarap principle ( 1). It is thus quite distinct from two other common uses of simulation. rand0misation tests and MARKOV CHAIN MONTE CARLO (for ftlting BAYESIAN MOOELS). IRe
=
IAckDowiedaemeab James R. Oupenter was supported by ESRC Resc:an:h Methods Programme grant H3332S0047. tided "Missing data in muitile\'c:1 models'.]
BaaaI, J. G. and Sarbr, S. 1998: Mo.-c:-Carlo IPIJIOXimation of booescrap vari.aaccs. The Anrentllll SlalaliC'i1Bl 52. lS4-7. CarpeD..... J. ad BHbtII, J. 2000: BOOlstnIp coaftdencc iJdm'als: when, which. ,,'hal? A pradicaI pidc for mediad 5Ialistici1m. Slalislica ill MttliciM 19. 1141-64. OatilDD, A. C. and ~. De V. 1997: Bootstrap mrlhotis and lheir appliflllion. Cambridge: Cambridge University PIas. EIna, B. aad TIbIIIIIruI, R. 1993: An inlm.clioIr 10 '''~ bootslrap. New York: OIapman & Hall.
boxplot This is a graphical display useful forhighligiatilll important distributional features of a variable. 1bc diagram is based on the five-number summary of a dataset. the numbers being the minimum. the lower quartile. the median. the upper quartile and the maximum. 1bc boxplol iSCOMtructed by ftrsl drawing a "box' with enck aI the Iowa- and upper quartiles of the data. next a horimntal line (or some other feature) is used to indicale the position of the median within the box and then lines are drawn from each end of the box lO the moll n:mole ObaemdiOM. One COII\'Cntion modiftes this last step by tnanc~ the lines to within (WlmaJtcd) poiatsgiven by the upper quartile plus 1.5 times the interquartile range (the difference between the upper and lower quartiles) and the lower quartile plus 1.5 times the intenauartile range. In this case. any observations outside: these limits are n:p~sc:nted indiVidually by some means in the finished graphic. Different compUIc:r packages may employ slightly ditrerent conventions for displaying exln:mc 01' outlyilll yalues. The ~sulling diapam schemalically n:pn:sents the body of the data minus the exln:mc obsenations. Particularly userul for comparing the: dislributional features of a variable in difrcrc:nt groups as illustrated in the figure. which shows the birthweighas of infants with severe idiopathic n:spinlOl)' disorder, classified by whether or not the infant SUl'Yived. For other examples see Altman (1991). BSE
3.5
-! .1iP
3.0
2.5
12.0 1.5 1.0
L_....!::==--__-===--_--1 Baby died
Baby survived
boxplat Birth..-eights (kg) of infants ,,,ilh severe idiopathic respirolory diseose syndrome (See also HlS"J'OGIWt. S'IDt-AND-LEAF PLor)
AICInan, De G. 1991: Pradital alalislit's for medko/ rrlWll'tlr. Londoa: Oaapman at: Hall.
Box-Cox transformation
See nAN5RlWA11ONS
Bradford HIli afterla Guidelines for drawing conclusions about causal relationships were proposed by Sir Austin Bradford Hill, Professor Emeritus of Medical
_ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ BUGS AND WINBUGS Statistics at die London School of Hygiene and Tropical Mc:dicine. in his adcImis to the Section of Occupational Mc:dicineofthe Royal SodelyofMedicinc in 1965 (Bmdronl Hill 1965). Bnaclrord Hill's guidelines drew on his many contributions 10 chronic: disease n:sc:an:h in Ihe post-war era. inciudililthe graundb~ng work with Richard Doll on the link belwc:en smoking and lung cancer. The following nine aspects ~ proposed for deciding whetbel' a statistical association might be causal: slmlgIb - rna;nilude of the association. as observc:d by measures such as the ratio of incidence rates; consistency - repcatc:d observation of the association in different populations and ci~umstanc:es and by diff~nt n:searchers: specificity - whether a cause leads toa single effect in a gi\'ell population: temporality - whether the cause pn:c:edcs the effect in time; biological gradient existence of a tn:ad or dosc-n:sponse curve betwcen the cause and effect: plausibility - whether the association is consistenl with currenl biological knowledge: cohe~nc:e ensuring that the inlelpn:tation or cause and effect does DOl conllict willi what is known of the natural history of the disease; experimcnt- existence of experimental rather lIIan obsenalionai evidence. such as through conductilll a nIDdomised trial ell' by introduction of a pR:\lCDtive measu~: analogy - comparison with previous ~search thai identified similar effect mechanisms. Bradford Hill did DOl intend these: guidelines to be philosophically rigorous "crileria' for causal infen:DDC. rather a basis for decision making that could lead to timely action for the good ofpublic health. With furthuaJDSicieration. some of the guidelines (e.g. "specificity') are less than universal in their utility and some commenlalon have proposed alternative criteria more finnly rooted in deductive logic (Weed. 1986). However, in prvposing these guidelines, Bmdfonl Hill advocated an approach of mWlll the besl use of the totality of available evidence: "All scientific work is incomplc:te -thai docs not confer upon us the fRcdom to igno~ the knowlc:dge we aln:ady have. or to poslpone the action it demands.' JGW
BradI'm'd HII, A. 1965: The enviroDmmt and disease: as:socialion or causalion? Procmli~ of,he Ro)'sl SOC~I)' ofMeJiciM sa. 295. Weed, D. L 1916: On Ibc logic of causal infmace. Amer;~tIII JoumaJ of Epidmlio/ogy 123.965-79.
bubbleplot nais is a graphical display ror line variables in which lWO variables ~ used to fonn a SCATIERJIIDI' and lhen the values of the third ~'ariable are leplgenk:d by circles with radii proparlionalto these values and ccntn:d on the apprvpriale poinl in the scauerplot. An example is shown in theftgum; hc:rethedalaan: for41 citicsin the USA and the two variables fonning the scallerplol are average annual tempenbln: and avenge annual wind speed. with the "bubbles' n:praenting the pollution level as measun:cl by the concenlnlion of sulfur dioxide in the air. The plot
suggests that higher pollution levcls an: associated with a combination oflowerannuallemperatun: and higher average wind speed. Mon: details or bubbleplots can be found in Everitt (2003). BSE
i
•
• (I)
12
-11
to
• •
0
G>
'g
1••
9
Iu
8
I
7
r
•• G) @®
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8 45
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55
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Average annual temperature (Fahrenheit) buhltleplot Bllbbleplol
0/ Qnnlllll temperalure tIIId wind
speedtlgQwt pollulion lel'elos mea:mredby sulphllr t/io.'Cide concenlration in the air fIN 41 cities in 'be USA (See also BIVARIA'IE IOXPLOI' and SCA11DPLOI' MATRICES)
E,..ut, B. S. 200): Modern mrdiml slllli"ks. London: Arnold.
BUGS and WlnBUGS 1be use of BAYESIAN METHODS in practical problems in medical statistics and other substantive an:as of application has bc:c:a hindered until ~lalively recently by computational aspects. In particular, the evaluation of integrals in order 10 obtain posterior marginal. conditional and pn:dic:tive distributions in many multiparamcler problems are nol usually analytically tractable and asym..olic. numerical integndiOD techniques or simulalio.based methods ~ n:quin:d (Bernardo and Smith. 1994). In many pnctical problems in medical statistics the lilnlc:tum and naIUn: oflhe models used havc made parameter estimation particularly amenable 10 the use of MARKOV OIAiN MONJE CARLO (MCMC) simulation methods and it is these that the software packages Bayesian inference Usilll Gibbs Sampling (BUGS) and Win BUGS (Windows version of BUGS) implement. (l.aIest versions at the: time of writing are BUGS 0.5 and Win BUGS 1.4 ~ fn:ely available fram www.m~-bsu.cam.ac.uk.)
BUGS and WinBUOS use the BUGS syntax. which is similar to that of S-PLUS a: R. to specify the likelihood and prior distributions for the stalistical modeJ in question. together with initial slarting values for the sampler (oillts.,
61
BUGSANDWINBUGS _______________________________________________________________ Thomas and Spicgclhalter. 1994). Wilhin Win BUGS the specification of models may also be in terms or directed acyclic graphs (DAGs) using the Doodle feature (see ORAPH. leAL )'IOOfJ.S). with the appropriate code being produced automatically. Additions to the most recent \'crsion of Win BUGS ( 1.4) are the ability to usc scripts so that WinBUGS may be used in 'batch mode' and impro\'cd graphics capabilities. together with calculation orahe deviance information criterion (DIC) to assess model complcxity and fit (see BAYESIA.'l METHODS). In addition. the suite of S-PLUS functions CODA (Best. Cowles and Vines. 1995) can be used to explore con\'Crgencc issues with output from BUGS and WinBUGS. Specific dc\'elopments of Win BUGS arc PKBUGS, which allows MCMC methods to be used for complex population pllQmracokinelidphumlarodYIlQmic (PKJPD) models and GeoBUGS. which is an add~n to WinBUGS that fits spatial models and produces a range of maps as output.
Since BUGS and Win BUGS require the user to specify statistical models in terms of the UKELIHOOD and PRIOR DISTRIBlT'J1m1S (see BAYESIA.'l METHODS). using MCMC methods in order to evaluate the model is only recommended for users skilled at undenaking Bayesian analyses and must therefore be used with considerable care -the manual even comes with a 'health warning'! KRA
Bernardo. J. M. and Smlt", A. F. M. 1994: Bayesian theor),. Chichester: John Wile)' & Sons. Ltd. Best. N. G., Cowles. M. K. and "Iae~ S. K. 1995: CODA COnl'ergence diagnosis and
outPII' analysis sojltt'Qre for Gibbs Sampler Olliput: Version 0.1. Cambridge: MRC Biostatistics Unit. Gllu. W. R.. Tbomas. A. and Splegelbalter. D. J. 1994: A language and program for complex Bayesian modelling. TIre Stalistician 43. 109-78. Spleplbalter, D. J.. Thomas. A. aDd Best. N. G. 2001: lVilrBUGS 'J'ersion 1.4 ruer manual. Cambridge: MRC Biostatistics Unit.
c calibration
Consider a situation in which we wish to mcaswc serum c:onc:enlnltiorw of hanaoncs. enzymes and other pmleins. for example. using such methods as radioinununoassays (RIA) and enzyme-linked immunosOl'bcnt assays (EUSA). 11an:c key questions in the development.of such assays IR (a) how does Ihc: expected value: (average) of the: assay response change as a funclion of the true amount of the target malerial in the senlm samples. (b) how does the VARIANCE (or STANDARD DEVIATION) of the USBy results change with the averBIe USBy n:sull and. subsequently. (c) how might we usc: a panicular assay n:sull to delerminc: the amount of the target maIerial in a new sample of' senun? We leave question (c) for the time being and concentrate on questions (a) and (b). Let the assay respDDse be Yand let the true: level orthe target material be X. We wish to clc:tc:nninc the form of the functionsF and G in the following two equations: E(YIX)
= F(X)
(I)
and
Var(YIX) = G(E(YIX»
(2)
Here we assume that the values of X IR known without !oIEASlIREMENT BUlOR. We an: concemcd with what is often ~fem:d to as absolule calibration. If we do not have access to the truth. but only have measun:ments using alternative assays. Y. and f20 say. then we ~ a:n:emc:d with the problem of comparative: calibration (for the lauer sec ME11IOD COMMIlISDN S'RJDIES). "JYpically. such a univariale calibndion study involves performing the assay proced~ (ideally with full. indcpendcat~ replications) on each of N training samples or specimens with known yalues of X. and then using various data analytic and modelling proceckRs to eYaluate the fonn of F and G. 11Ic: statistical mc:Ihods might be fully panmc:tric (Htting linear or nonlinc:ar models, for example, with an assumed parametric model for the wriancc:) or nonpanmc:lric (esSCDlially filting an ubilrarily shaped smooth dosc-n:sponse curve). Suppose: an analytical chemist wishes to use some fonn or absorption spectroscopy to study the composition of. say, certain body Ooids. He or she is likely to use meas~mc:nll or many peak heights &om such spectra 10 measure several substances simultaneously. This activity is the multivariate analogue of the univariate case; i.e. multivariate calibndion. Technically, multivariate calibration is much IIICR dimcult than the simpler univariate problem. but the ullimale aims and logic an: similar. We stall with the latter and then brieRy discuss the former. £rrqdDpllldie C~ to' AlNItaI SllIIis,;a: S«OIIII Edilim cJ) 2011 JohD Wiley 1\\ Sou.. ....
Instead ofdealing with the technical complexities offilting nonlinear models with heterogcac:ous error distributions. we will consider an example that. by comparison. appears to be: quite simple. Suppose we hayc a simple colorimmc assay fOl' urinary lIucose. We obtain a series of specimens with known lIucose concenlnliorw (X) and then measure the: absorbance using the mevant assay procc:dwc. We assume thai the calibration function F is a slnight line and that the variance of the Y measulmlCnts is independent of X (i.e. the 'enor' variance is constant). Filtin, a simple linear regRssion model for Y using ordinary least squares gives us estimates of the: inlen:c:pt (u) and slope (/J) of the slnlight line relating X to Y. Having answeml questions (a) and (b) usin, the: simple: rqressionanalysis. we now move on to question (c). Suppose we an: presented with a new urine specimen and ~ asked to ddcnninc its glucose eanlenl. 11ae classical method of estimating the unknown X fram our measurement. Y~ involves using information from the abovercgessionof' Y.X.1bc: requircdc:slimate isgi'Ven by:
(n
x = (Y-a)/IJ
(3)
An alternatiye is the so-called invc:ne estimator suggeslCd by Krutcbkoff(1967). This involves using the original X. Ydata to rcp:ss X on Y to obtain estimales of the: intcra:pt (y) and
slope (1). and then simply using these panuncler estimates 10 pmlict X giyen a new fl' i.e.:
.
X=y+AY
(4)
For details or the properties of these: two estimalon. see the review by Osbome (1991). To illustrate the ideas of multivariate calibration. consider a n:latively simple ellample. SuppaIC we wish to measwc the concentration or a particular metabolite in the blood (X) but we arc now able to usc, say, thn:e different colorimetric assay pmcc:dun:s to olMain yalues Y•• Y2 and f s• Assuming that the thn:e carn:spanding calibration curves (F.. F~ and F~). as before, are all straight lines (but with ditTen:nt intcn:epts. slopes and "c:nar. 'Variances) we CaD use MULTIVARIATE UNE..o\R REORESSJON (orlhree separate n:grasions) in order to estimate the panunclers or the thn:e calibration curvcs. 1hc classical approacl1 to the uscor. new set oflhn:e measurc:mc:nts (Y•• Y2 and Y,) on a DeW specimen 10 pnxlic::t an unknown X is the: mulliYariate generalisation of the univariate problem. DeWls of multivariate calibration IR well beyond the scope of the present article. however. and readers ~ refClRCi 10 Thomas (1994) and Naes el al. (2002) fOl' further information. Consiclc:ring our prescnl example:. one simpleappralU:h
Edited by Briaa S. EYeritt and ChrisIGJlh« R. P'IIImeI'
63
CAUPERMATCHING _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ __ (particularly if we are prqJBrCd to assume ClGftditional inclepeadcnce of the Y values) might involve estimating the unknown X using each or the YI' Y: and Y;t values separately (in each case usiag equation (3) above) and then producing a weiPtcd average of these thR:e estimates, with weights proportional to their estimated precision. An example of the inYCn1e approach would be to produce a multiple regn:ssion to prc:dict the unknown X from Ihe three Y measurements. This has ob\'ious lC:chnical drawbacks, howe\'Cr. because or MUIllCOWNEARm' (high correlations betwcca the lhrc:e Y values). One possible solution involves the: usc of principal components regression. A PRINCIPAL COMPONENI'S AN.u'YSIS is carried out on the Y values and then one or man: of the resulling components are used to predict the unknown X. Fwdaer details or principal components regression and alternative analytical stnlCgics can be found in Tbomas (1994) and Naes el D/. (2002). Whalcver method of prc:didion is usccl however, it is important in bath univariate and multivariate calibration problems thal the performance or the predictions arc adequately evaluated. this might involve validation using a test sci of new X, Y values or internal cross-validation (use or the LEA\'E-ONE-CX1T CROSS-VALIDATION approach. for example) using the original lraining set. GD
Kntdlbft',R. G. 1967: Classical and invcne lCp'CSSioa methodsof'
rewa, Dan.. T. 2002: A ruer-/riendl, gllide 10 nut/lilYll'iale
calibratiCJll.ledllORfetrit~ 9. 425-39. NaIl, T.. 1.1aRa,T..
T. aM
ralibralion tmd citmijiC'QlioIr. OUchcster. UK: NIR Publicatians.. 0IIt0rae, C. 1991: Statistical calibration: a nwicw. InlmllllioMI StaliJliCQI Rent.., 59, 309-.36. nama., Eo V. 1994: A primer on mullivariale calibration. AnIl/yliml Chemislry 66. 79SA-804A.
caliper matching
See MATCIDNO
canonical correlation analysis This technique establishes whether relationships exist between a priori groups or variables in a study. For example. in a study or heart disease, we might ask ir then: is a connection between penonal physical charac:lcristics such as age. weight and height. on the one hand. and the systolic and diastolic blood pressures or the individuals. on the odler. Altc:mativc:ly. in chronic depn:ssion. a study might be aimed at uncovering rc:lationships between personal social and financial variables such as gender. sse. educalional level. income and a range or health variables induding various indicaton of depression. In anothu example. a public health survey might be C1Jftdueted to explore cOMections between housing quality variables and indicaton of different illnesses. A first attempt al analysing the strength of association between two ,TOUPS of variables (e.g. between hausing quality and illness) might involve examination or all COII'CIalions betwcca pails of variables.. one from each group. Howevu. ir cadi group contains man: than just a rew variables. such an approach is bound to lead to conrusion.
Ideally. one would like 10 n:place each set of original variables by a new set. in such a way that the new variables were mutually uncOl1'elaled within sets and just a few of them exhibitc:d correlation betwcca sets. Canonical correlation analysis takes just such an approach. and finds optimal sets or linf!DT Irllllsj'oTmQI;olU or the original variables. one ror each original group of variables. Suppose that "I. II:••••• Uk an: the InIDSfonned variables ror one sci (say. the housing quality variables). while ",. "':•...• I'k an: the transfonned variables ror the other sci (say, the illness variables). "Optimality' is defined by requiring the correlation betwcen "I and ", to be as Iarp: as possible among all linear combinations of the original variables. that bc:twecn II: and 1'2 to be the nextlarp:st. that between u) and l':s the thinllar;est and so on. subject to Ihe rollowing constraiD15: II:• •••• an: mutually UDCGITClated: 1'1. "2••••• If.. are mutually uncorn:lated: and any",. pair is uncom:latc:d when ; #= j. It is clearly nat possible to have more (uncorrelalcd) transronncd variables Ihan then: were original variables in a set. so the number sorpain that can bedcrivcd is equal to the smtzl/eTofthe numbel'sororiginal variables in the two groups. The effect of canonical cOl1'elation analysis is thus to channel all the association between the two groups of variables through the n:sulting pairs of Unear combinations (u""')' (U2.I'2)' .... These derived variables are known as t:Dnonit:DI WlT;Dles. The only nonzero correlations n:maining in Ihe c:orrclalion matrix of the new variables an: those between conaponding pain or canonical variates.. i.e. between u, and ,., for; = I •.. -•.s: they an: known as the alIIOlfit:tJ1 t:orreIDlwIf,s of the system. Mos. computer software packages that conlain multivariate slaliSlical prot'edurcs will conduct such an analysis. They will also quote a significance level against cacl1 canonical conclalion. appropriate ror testing the NUlJ. H\'FOI1IESIS that all succccding population canonical cOI1'elations are zero. Such significance levels should be bellied with some caution, as lhey rely on Ihe assumption that the data follow a MULTlVARIAlE NORMAL DISTRIBUIlON. Nonetheless. the number or signiracanl canonical conclations is usually laken to indicate Ihe number of (independent)conncctions that ex is. betwcen the two groups or variables. Inspection of Ihe aJCfftcients or each original variable in each canonical variate may also proVide an interpretalion or the canonical variate in the same manner as interpretation or principal components.. which may help to identify the natun: of the conneclion between the groups (sec PRINCIPAL COMJlONENT ANALYSIS). However. again a cautionary note is in order. because such intellRtation is not quite as straightrorward as ror principal components. The reason ror the complication is thai there may be very diverse VARIANCES and covariances (sec COVARIANCE MATRICES) among the original \'ariables in the two groups, which affects the sizes of the coeflicients in the canonical van-
"I.
"I
"k
_____________________________________________ ates. and Ihere is no convenient normalisation to place all coefficients OR an equal fooling. This drawback can be allevialcd 10 some extent by rabictinl interpretation to the :lIQntlartli.d coeOicienlS.. i.e. the coemcients lhatln appropriate when the original variables have been stanclanlised. but nevenheless the problem still n:mains. To iIluslrale the technique. consider a canonical conelation analysis bc:Iwcen the 'health' variables ancIthe 'pcnonal' variables in the Los AftlCles clepn:ssion study or 294 n:spoadcal5 pn:senlCd by Aftft and Clark (1984. Chapter IS). The four 'penonal! variables \VCR: gender, DIC. incCHDe. c:cIucation level (numerically coded fram the lowest. 'leIS than hilh school'. 10 the highcsl. 'finished doc:lOrate'). while the IWa 'health' variables we~: CESD (the sum of 20 sepande Dumerical scales measurinl clift'en:nt aspcc:1s of clcprasion) and health (a numerical sc~ measuring 'general health'). The c~ma matrix bc:twc:ea these variables for the sample is showa iD Ihc: table. canonical correlation ....., ... ConeIafion mattix for Iwohealth andlourpersona/VIIIIIIbIBs in the LA ~ sionstudy CESD HeQII" Gentler Age &iMmliDn Income 1.0
0.212 1.0
O.llA 0.091 1.0
-0.161
alGI
o.ow 1.0
-0.101 -0.210 -0.106 -0.208 1..0
-0.151 -0.183 -0.110 -0.192 0.491 1.0
C~R&4ECA~REM~
worth. TIle conapondiag canonical variates In: fI2 = O.I99C£SD + O.288Hetlllh 1'2 = 0.396Gentler-O.443Age-0.448Edrlt:tllion
-O.ssSIRt:on,e Since the higher value of the gender variable is for females. the interpn:1alion hen: is lhal ~latively yauag. poor and uneducatc:cl females ~ aaacialc:cl wilh higlac:r depn:ssion SCOleS and. lo a lesser ellteal. wilh poor ~eivc:cl health. Thus Ihe~ are two inlClplelable 'dimensions' of cannCCli_ betwa:n the 1W0 sclsofvariablcs. A SCAmllJll.Ol'ofthe scores of ~spoadents &pinst each pair of canonical varialeS would help to identify any anomalous individuals in the sample. A further inlercstinJ application of canonical ccx-mali_ analysis occurs when there isjusl a single sct of variables. but they ~ measun=d on individuals in a number of a priori distinct poups or populations. Forcxample. a set of signs or sym..OIRS XI. X2 • ••• , .t'~ is observed ma a sample of patients suffering fiomjDunclice and each padent isclassifiecl inlOone of I illnesses thai have lheeXlc:mal manifeslali_ orjaunclice. We can thus define a sct of indicator variables 11. 12' •••• )'. that specify a palient's illness. by selling the values 'i= I. 1./=0 (j:F i) for a palicnt suffering fram illness i. A canonical com:lalion analysis with the x values as one SCI or variables and Ihe 1 values as lheolher sct ofvariablcs willihea produce the linear combinations of the .y values thai ~ most highly com:lalc:cI with linear combinations of the poup indicator variables. Since Ihe lauc:r deftne the best way 10 view group dift'e~nces. the fonner an: just the canonical variables tbal best discriminate belWcc:n the I grvups of individuals (see DISCRIMINANT RJNCI10N ANALYSIS).
He~
the maximum Dumber of canonical variate pain is :1= min (2. 4}=2.1be fint cllDllllicai cam:lalion turns GUlto be 0.405 and this Ih'CS a sipificance level P < 0.00001. II might be arguc:d thai lender ancI c:cIucalion ~ unlikely to have normal distributions. so Ihis SignificllllCle level should not be laken tao litemlly. Neyenheless.lhc:~ does seem 10 be strong evidence thallhe ftJst canonical cam:lalion is significant. The: cam:sponcling canonical variates, in lenns of slandanlisecl original variables.~: "I
= -O.490CESD + O.9I2HeQII"
= O.02SGe",lo + 0.87IAge-o.383EtluCllliM+ O.082lnl:o",e High coefticients com:spond 10 CESD (lICIatively) and hc:alth (posilively) for the ~c:aVc:cl health variables and to age (posilively) and c:cIucation (Relatively) for the penonal variables. Thus n:latively older and unc:ducatc:cl people Ic:nd to SCOle low in terms of clepJasion. but penx:ive their health as matively poor. while ~lalively younger but c:cIucaled people have the apposite hc:aIth pen:c:plion. The second canonical conelation is 0.266. which has a significance level P < 0.00 I so also carries interpretalive 1'1
Finally, the variables in a slUdy may fall inlO IlleR than two tI priori sets anclsome genend between-a mea5tR of associalima is requiral. Various possible definitions of such associalima may be made and. consequently. the ideas or cllDllllicai COlRlation analysis may be gcmeralised iD various ways. However, such generalisali_ is quite complicalc:cl and inlerpretation orthe n:sults becomes much more problematic. Gnanadesikan (1997) pnmdcs a brief overview and further ~f'en:accs. WK All, A.A. ... CIIIItE, V. 1984: Compuln-tlitletl _Ii,trille _lysis. Califomia: Wadswadb. O.........Ire., R. 1997: IIeltrods /« Jllllwimllllllll,lis tJf mulli.triJle obm-tVlliou. 2nd cditian. New York: Jalut Wiley a: Sans. Inc.
canonical variates
See
CANONICAl.
CORIlELAnONS
AJW.YSIS
capture recapture methods
"Ibis is an altemalive
appruadJ to a census for estimating population size
that operates by sampling the population several times. 65
~~EC~REMB~
_____________________________________________
idenlifyilll individuals who appear mCR dian once. Captun:-n:ca~ mdhods ha~ a long hislDry dalilll back to 1786. whca Laplace used such a technique lD CSlimalc the size of lhc 10IaI papulalion of Francc. Traditionally. captum-R'apleR melhaclolagy was primarily focused on wildlife populations. bUI has increasingly been applied to human populations, particularly within epidemiological situations. Within the ecological Reid. Caplum-nnplUle experiments involve observers going inlD the field and m:ording all animals ht an: absc:ned (either visual sighlings 01' trappings) at a scquc:ncc of capture e~1s. On lhc initial ca~ event, all aaimals that an: obsened an:: m:orded. uniquely marked ad released back inlD the population. Al each subsequent captureevcat. all unnuukc:d animals an: recorded and uniquely nuutcd. aU markccl animals an: lUanied and all animals released. The data from such an experiment 1ft simply the ~ of captlR histories for each individual animal observc:d within the study. Each iadividual caplUrC history is typically rcpmICntccl by a series of ZCIOS and ORCS. when: the 0 and the I denote lhc absc:acc or presc:ncc. n:spcclively. or lhc individual at each capture event. Then: an:: generally two fonns or models for captum~Caplure data: closed and open. for which there have been • series of models proposed. Closc:d models assume hllhe population is 4Xlftslanl thmughout the study period. with no births. deaths or migrations. whcn:as apen models allow for these traasitions in the populaliOD. Generally speaking. the panunctcrs of inlcn:st diller between the IWo models. Forexample. within closed populalions. the total population size is geacrally of particular inten:st: convenely. far open populations. parIII11CICI1s of interest may include birth rates. dcaIh rates. migration rates and/or pnxIuctivity rates. We initially. bricJ1y. consider the c:aplum-~apleR methods often consideml fOl' wildlife dais before 4Xlftsidcrilll in fUrther dc:tail epidemiolopcal models. Forcloscd populations. Otis el DI. (1978) described a series of different Caplun:-n:ca~ models. relating lD possible hclCrogcneity in lhc capture rates as a rault of time. Irap n:sponse or individual elTec:ts. 10111 and Brooks (2008) ha~ incorporated these madels inlD a Bayesian framcWOll. Mix.tun: models have become inc~asingly popular lD model individual heterogeneity (Plcciger.2000: Morgan and Ridout. 2008). Additionally. then: ha~ been a series of models proposed for open populations. dependent on the paramcIcn of interest. with perhaps the most widely used beilll the Cormac:k-Jolly-Sebcr madel. whIR lhc sumval rab:s an:: of primary interest. ad the Amason-Schwarz model. which incorporates multiSlnlIa cIaIa. Recent advances include the generalisation lD multiC\'ent models (Pradcl. 2005). where the SlaIc of an individual may only be partially observed. Within the epidcmiologicallitcratun:., closed populations an: usually modelled. with the lDtai population size of particular intcn:sl - and this is whal we shall focus on here.
capture-recaplure methods Example of an inc0mplete contingency tlJbIe, with three SOUICeS: A, B and C. The entries n.- denote tire number of individuals obsstved in the given cell, where 011 tepf8SBlJls libsencelPl8SeIICe on the given list. The cell ntIDD is unobsewed and hence unknown
C=I A=l A=I A=O A=O
8=1 B=O 8=J B=O
"I ..
c=o
IIIDI
110 "lliao
110..
11010
11001
lllIDO
For example, many IR8S of scientific n:scan:h focus OD the estimation of papulation size: fiom the number or susceptibles lD a given disease. lD the number of drug addicts in a panicular area or the number of injuries sustained in the workplace. However. it is usually impossible lD enumerate each member of a populalion. possibly clue lD their number (e.g. the number of web pqes on the intcmc:t) or whca the papulation is ·hidden' (such as the number of injector drug usen). Thus. data 1ft often collected in the fonn of a series ofincomplctc populalion counts using a variety of sources 01' lists. Each saur= ~spDnds to a capture event and an individual being IaXJI'dcd by a gi~ SDU~ com:sponcis 10 being observed at ht captun: cvcnt. It is assumed that each individual is uniquely identiRable by each soume. 11Ic:n. the data 1ft simply the capture hislDrics of all individuals o. served. The clata an:: usually 5ummarisc:d in the fann of a contingency table., when: k is the number of sources. and the cell cables corn:spond to the number of individuals thai an: observed by each combination of SlJUn:es (i.e. the number of individuals observed with the same capture history). Cleady. lhc contingency table is incompleac since the number of individuals belonging to the papulalion but not absc:ned within the stucly is unknown (sec the lable. for example). Unlike the ecological application die soun:cs do not usually have a temporal scqucncilll as for the captun: events and so dilTcmat models ha\'C been developed within Ihe epidemiological application. Within lhc epidemiological field the captum-recaplure approach is sometimes callccl 'multiple ~ systems' and the corresponding estimate of the total population refem:cl to as 'Bernoulli census estimates· or 'uccrtainmcnt c:orr=ted rates'. 1be most common appI'OIIC.h to analysing epidemiological data of this san is via the use of LOa-LINEAR MOOELS. introduced by Faenbcrg (1972). In these models. the logarithm of the expectccl cell count is expressed as a linear function of panunclel'S. These parameters relRSCnt main cft'c:cIlcnns for individual soun:es and associations bc:Iwccn two or ~ soun:es. Thus. these models allow for interactions between diffcmal soun:cs.. The model assuming indcpcncIcnt'C betwccn each soun:c is simply a special case:
t,
______________________________________________________ QUDOGMM .willa DO inb:ncIions JRICDL '11Ic:n: are 85_0y a DUmber of possible 1..-IiDeal' models lhat CaD be lilted to lhc
dada. each specil'yilll clifl'en:al sets or interactions bctWC:CD
the soun:cs. Tradilionally, classical aaalyses coasist of initially lindilll the model which pm\'idcs the best fillo Ihe .... _11& ror eumple, UDIJHOOO RAllO 1f.S1'S aadtor iDformaai_ criteria, such as AlCAllCE's INRlIMATIOX auTERION (AlC) or BtlyesiDlr in/Dmllltiolf mleritnr (aIC). Once lhc CiYCD madc:J has beell selected, the Ialal popuIaiiOD is csIiIaaIc:d .sinc MAXIMUM LIKflJIIDODES'IIMATIOX fardac miSlinlceD. cambinCd with lhc observed number oI'individuais (sec. forexampic, HOlIk and Rc:pI, 1995). Reccndy, Bayesian appmaches have also beca deveJaped for ftllinc 1og-liDe. madels to Ihc cIaIa, and ill )NIIIiaI1.1he issueof .....1choice (KiDl amlamob, 2001; KinI el QI. 200S). 'I1Iis approach also allows the calc.11IIioD or a modcI-avcrqcd estimate of the IaIal papulalion. I1:I1KWinc die ....I-clepcaclcace pmblem lhat mayarisewheD ....y
a siagte model is chosea on which 10 basi: infcn:lllx:. AIlerllllliw: appnNIChc:s to .sinc 1oI-1me. models iDclucle: 8SC 01' the Rasch model (see Caniquiry and FacDbeq. (998) in anIer to madel possible heterop:DCily iD the papulation and also IBleat class models when the individuals CaD be categorised inlo ditren:al subpopulations. RK
CaniqaIrJ. A. L
............. 5. It. 1998: Rasc:b IDDIIcIs. In p. ... Col. T. (cds).. Erreyt:/1Ipftiia D/ bitutlllillirs. CIIic:Iaa!ilCl': John Wiley" So-. Ltd........... 5. It. 19'12: 'I1Ie Anni~
mulliplc RCIIIIIIR OCIISIIS for clDlcd .,..11Iians ud iDcampIclc 'i' eoaIingcacy IIbIes. BitHnelriktl 59. 591-603• . . . , ........ RIpI, .... 1995: ~ mcdaads in cpdanialol)':
_sis
IDCIbods and limilalians. E,ilknliDllI,itlll Rnin.. 17, 243-64. KIIIIt ..... IInab, s. P. 2001: Oa abe Bayesian or papuIaIionsi&.Biotnelrikll88. 317-36. KIDa. ..... ~s. P. lOO8: On Ihc BayesilD esIimaIian or a closed papailliCII size in Ihc pn:seDCC of IIclCmpadly ... madel 1IIICCItIialy. IJitllMlrks 64, 81~24. KIDI. a., BInI, s. at., BnIab, s. P., Ba.J. o..... y • ....., S. 200S: Prior iDfOllDllliDn iD bebaviDlaal c~ ftlCapbR IDdhads: c1cmopllllly iaftDlD:CS injecIDII' pnIpeDIity ID
be listed GIl data!ICIIRCI1IIId lhcirdrupclllCchna...UIy.A....... JOIIIfIIIloJEpiMmitJlIIg)' 162.094-'103. OIII,D.a.., . . . . . .,K.P.. WIlle, o. c. ... A8dInMI, Do .. 1971: Stalislieal iDfeRnce fftIIa aphRdIta _ closed IIIIiIDII papallliaas. Wi/tli/, 62. 1-135. U ........ J. T..... ....., M. S. 2008: A new mixlUre model far aphR hdcqcaeil)'. JauraaI or the Royal SlIIIislicai Socicl)': Series C 57.433-46.......... s.lOOO: UniW maximuIn likclihoad csti_ta ror closed ~ IIIOdeIs IIIiDI mixllRS. BitJlntlTks 56. 434-42. ......., .. 2005: tttultic:Ycat: an exImBian ofmuhislalectplllla-ftlClI*R models IOUllCCllaiaSlates. B-.tI'icr61,442-7.
II""",,.,.
carry-over CART
See CR05SOYER 1RL\U
This is an 8CI'OJIym 'or clusificlllion aad 11:p:s-
siOD 1n:C. See TIEE-mtUC'IUlED loIEIIIOD5
cartogram This is a diapam ill which clescripli~ slDlislical iDformatiCIII is displayed on a p:opaphical map by means or shadiag, by usilll a variely 01' diffi:n:Dt symbols or by SOllIe IIICR illvolved pmc:ecI&R. Two examples in . . - s an: liven. A dcscripti_ of bow cllltognaas may be COll1InIcIc:d is given in OuseiD-Zade mad Talcanov (1993). SSE ISec aim DISEASE a.u51I!RIKOJ
CIIItognun CstIogram oflfe expedBncy in Ihe USA by slate.
<10 -10 yeats or less, >ro - mote ,han 10 yeatS 57
~sruDl~
________________________________________________
cart..... 1996 US population CIIItogram (III states aRl. resized telatitle 10 their population) Qaela.Zadt, S. ad l1~.V. 1993: A
coaslrlldiac
CDDtlauaus
DCW
cutopllDS- Geo,rtlpII}' _
' 'formtl';. S)'SImu 20. 167-73. caa-cohort studies
meIbod lor Gtogmpbic
Sc:e CASE
case control studle.
'I1Iese an: slUclic:s in which a group or people with the disease of intcrat (the cases) is CXIIIIpImI with a paap without the disease (the cantrols). ExpasUR tolherisk factarofinICn:Sl is then asc:cnainecl in all those m:ruitcd 10 the study and the CXpcllUle levels or the cases an: anpan:d to those of abe coatmls. Difl'erillllcvels of exposUre between the cues and conll'Ols indicate that the exposure is associlllCd with die disease:. Such Iludics arc padic:ularlyappmpriatc for rare disea.,s for which foDow-up studies arc inappmpriale. as insufftcic:llt cases of the disc:asc wauIcI to provide suflicieatllatistical FCM'ER. It is ilDparlant at the outsc:I to ..~ a clear deftnitioa of the type: ofpcl1lDD who is e:liJibIe to be • case. Issues Ihat nceclto be coasideled include:
_se
I. 'The tkjinilion. DIIM tlisetul!. Can Ibis be broadly dcftnc:cl aris a specific: subtype orthedisease the lOcus ofink:n:st? Par example, in a sIUdy of Ic:akaemia a clecisiOD nc:ecIs to be aaadc as to whc:1hcr all cues of leukaemia wiY be included or only • spc:ciftc subtype such as chronic myeloid. 2. The till! l'IIIIge t1/ ,he (YIS'Q. Some diseases .an: lilcely to ha~ difl'~nt causes at difl'erent ages. 3. TM sex of lire ~tDe~. Por some disordc:n. it would be appmpriale to n:slrict to one: or GIber sex. For eumple.
while cues ofbn:asa cancc:rcID arise in men, Ihe adiology of these is lilcely to be very diffi:n:at from that of Ihe disease in women. 4. Indtiml. prntUDlI.or de«lUeti auG. b is usually prefcrab~ to m:ruil cases when they an: cIiaposccI (incideal cases). Howe'VCl'. far diseUes thai arc very rare il CaD lake too loq to n:cruit 5uflicic:llt cases. They can Ihm:rCR be: supplc:mc:nted by cxistiRl (JRvalent) cases. Howcver. far diseases that can lead to death.·the pew)cnt cases will only n:pR1CD1 Ihc: survi~. To avoid survivor bias.. deceasccI caSes CaD be: iacludcd if the: nexl-of'-kin CaD pavviclc the appmpnate information. on the eqMISUR ofinlclat.
s.
HospilQI D~ co"""",,;I,. CtI• .r. A clec:isiOD nc:c:ds to be: laken as towhi:n: thec:aseSIR to found.trthe disease is of'
such a naIu~ thai all caseSIR likely to COIIIC to hospital (e.g. bn:astcanccr). then the hospital may be an 8pIIIOpIiaIe recruibnent Iomticm. For diseases that are o~n natal in the community. such as back pain. n:cnaitment Iium hospital wiD only include cases aI the mast SC:VC:~ end or the· disease. speclrUlD. Equally, besides. the choice of cases. lIM= an: impadDDl considerations for the selc:ctioa of controls. who should be dmwu from Ihe population -at risk of bc:c:oming asses. In 1heoIy~ the cases and conlJolscan be considcn:cl as beiDg part ofa Iarp hypothetical COIICItT~ Those who develop Ihe cliseaseare dlecasc:s, ad those who hawnlDl acquiml il fann the pool fiam which .the conIrols an: drawn. Thus controls should be drawn can:fully fram the graup or people: who would be elassificd as cUes if they happened to~1op the disease.
__________________________
Controls should be wilhin abe same age range as lhosc chosen for the cases. and ir only one sex is being considered for thecascs abe same n:sbiclion should apply lO lhc controls. If the cases are rccruitc:d in hospitallhcn abe controls may also be recruited from the hospilal or from the communily defined by the catchment area or abe haspilal. Any exclusion criteria applied 10 the cases must also be applied lO the controls. and the controls must be al risk of developing the disease. For example. in a case-mntrol study ofendometrial cancer. il was importanl"'at women who ha\'e had a hysterutomy. and thus no longer had an endometrium. were not included as controls (Barbone.. Austin and Partridge. 1993). Increasingly. matched case-control studies are being eondueted (sec t.L\TCHED SAMPLES). One or more controls are chosen for cach case. matched as closely as possible to the case ror various radors that ~ not of intrinsic intcn:st to the study. Common matching factors am age and sex. Thus for each case. a control of the same age (topcrbaps within one year) aDd abe same sex would be chosen. ~to-onc matching gives rise to a matched pair study. To iDcrease the statistical poweI' of abe study. more than one conbol can be chosen roreach case. This is particularly useful if the disease is rare and it is hard lO Ond sulTacient cases. However. it is mrcly wOJth studying marc than four controls pcl'casc. as the elTort spent in collecting abe dala on abe exlracontrols tends to outweigh the minimal inc~ in power. Frequently. the exposures will be assessed by QUES1KJN. NAmES. This can presenllogistical diflicullies irthe cases are yel')' sick and sometimes (as withdcceascdcases) abe next-ofkin need to be questioned im'lcad. For example. in a casecontrol study to examine abe risk of sudden infanl death syndrome in relalion to used infant matlresses, all Ihe expos~ data were collected by questionnaire (Tappin el 01.• 2(02). ExPOMR 10 a used infant maltMSs was assessed by asking parents about routine night and day sleeping places and ascertaining the state of the mattress and whether il was new for this baby. Other studies have been able 10 link n:cords with data held on the individuals. For example. a study of Alzheimer's disease in relation lO levels of aluminium in drinking walcr was able 10 utilise n:conk from the water companies loascerlain lhc aluminium levels in waterpipcd to each address aI which abe cases and controls had lived during their lives (Martyn elol. 1997). A particular concern in case-conllOl studies is the possibility ofJlECAl.L BIAS. particularly when obtaining information by questionnaire from the cases and controls. 1be cases ~ likely lO have thought about the possible causes of lhcir disease. whereas the controls will DOl. Thus the level ofn:call of past exposures may differ bc:Iwc:en cases and controls. which may lead to spurious differences in exposure between the two groups. One of lhc mast difficult aspects of a case-mntrol study is ensuring that the choice of COnb'ols is appropriate. Controls
CASE~ROLSTUDIES
that arc not rqJresenlalive of the population al risk of the disease will lead lO biased findings (sec BIAS IN OBSERVAYIQN,\L S11JDIES). An example is when the cases ~ asked to choose a friend to ad as the control. Such an approach tends 10 maximise the n:sponsc rate in the controls (as the controls are usually willing to help their sick friends). However. if the expos~ of interest is related to wort or leisure activities or lifestyl~ then the friends will be more similar to the cases than lhc a\'erBJ:e penon in the population at risk. Thus owmnolcbing or conbols to cases takes place and little difference may be rOlDld bc:Iwecn the exposures of the cases and the controls. Any association between the disease and abe exposure can therefore be missed. Issues ofBLO\S ncc:d to be addn:ssed at the design sta;e of a case-control study as no adjustmenl can be made in abe analysis to take accolDIl of it. In common with all epidemiological shldies. "onj'ounding is an issue that has to be considelal in casc-contml studies. A confounding factor is one that is reJalcd both to the disease IDlderstudy and thcexposun:ofinlercsl. Aceountcan betaken of confounding factorsal the analysis stage. bul it is important at the design sta;e to identify and collect as much information as possible on an putative c:mfounding factors. Common confounding factors are age and sex as these two factors an: invariably related to any disease and to most exposun:s. Marching at the design stage on one or marc confounders provides a way of removing abe effect or these confounders and so adjustment for them is not needed in the analysis. The appropriate method oranalysis depends on the type of case-conlIOl study employed. 1be analytical methods for matched casc-conbol studies differ rrom those for unmatched studies. and it is important lhatabe appropriate methods are employed to a\'Oid bias in the results. Basic methods of analysis in unmatched studies arc describc:d next. Estimates of risk of disease in lhc unexposed and exposed groupscannol be obtained fmmcase-control studies. because the case
ca_ control studies A 2 x 2 tsble for comparing a+ c cases with b+ d controls
Exposed Unexposed
Cases
Conlrols
Q
b J
C
1hc ODDS RAllO is the ratio of the odds of exposure in the cases (01,,) to abe odds of expos~ among the controls (bid) and thus iscalculatedasodfbc. Oddsratiosabcn'e I imply that abe exposure is associated with an increased risk of the 69
~Olgru~ES
__________________________________________________
disease whcn:as a YBlue below I indicates that the exposure may be pnIICCtiYG. As an example.. consider a study or cod li\lCl'oil in infancy in n:llllion 10 chiid-ollllCl 'J)pe I diabc:acs (Slc:ac and Joner" 2(03). The n:sults an: givea in Ihe scc:ond bible 1111: odds ratio is 197 x 1341(777 x 318)=0.66., indicllliagllaatcod liva-ail appears 10 pntIcct against chilcl-onsc:t diabetes.
li\lCl' oilleadillllG lower odds raIios. 1bc chi-sqWR test far tn:nd leads to a significancc level of p < 0.001.
call control studl. Case conttol study dallIlICCDffJinQ to lin 01rlinIlI exposUI8 Cod liver oil in lsI yelU ojlij'e No
Yes. 14limcs per \Wdt Yes. ~5 limes per week
Cod lilter oil ill
Ctue.s
COIIlml.s
0tJtI.s ratio
311
834 224 553
I (rd'ance) 0.70 0.65
60
137
Corrlro/s
INI ,wr tJf I(le
Yes No
197
m
311
834
SIaIIdanI analysis of a 2 x 2 table uSIlq; a OI-5QlWtE TESI" can be pcrfonnc:cl to test whether the odds nlio dilTen signilicandy fmm I. The 95 ., COMFJDEXCE INI'EIlVAlS can be deri~d usilll a varidy or approxinudc methods. 1'1Ic most
sophisticated methods taplin: ib:ralive solutions but simple methods such as that praposed by Woolfin 1955 (sec Breslow and Day. J98O; ScblessellDllll. 1982) provide n:asoaable appruxilDlllions. His method involwscalculatilllthe approximate VARIANCE of dac naaurallopridun of the odds mio as: 1 1 1 1 -+1"+-+a .n r II
More sophisIicatc:d analyses ~ possible usilll LOGIStIC REORESSJON. This allows assessmenl of cxposum on a con-
tinuous scale (rather than n:quiringgrauping into levels' as ,,'CD as aIIowilll for Ihc: etrccls of confounding factCIIS. 1'1Ic coc:fticients obtained in the logistic regn:ssion model are the logarithms of the odds mlios. and the actual adds ratios and their confidence inlc:n'als can be raaclily obtained. In a matched study, the conlrOls have deliberately been chosen 10 be mon: similar 10 Ihe cues than those gc:ac:ralJy at risk or the disease.. This has to be n=cognised in the analysis. The analysis of malched lIudics il man: complex than far ul1lll8lchcd sludic:sand in the discussi_ of the basic analysis., only mab:hcd pain analyses will be considered. The analysis focuses _ the pails rather than the individuals contributing to the pairs and lhe standard pn:scnIaIion of the daaa is as follows:
and then obtaining the 95 ... 4.DIficlcnce ialCrVal of the nlllUrai logarithm of the odds ratio fmm: log(OR)
=
Conlrol
1.96)C J'var[loI(OR)]
Taking exponentials orlhe two .aulting values gives the 95 CJ, confidcace inlCnBl for Ihe odds ratio. In Ihe example above the chi-sq~ test gives a value of IS.3~ indicating p < 0.0001 and a 9S fJt coaftdc:nce inlcmll for the odds ratio of 0.54 10 0.81. Thus this simple analysis indicates a sIrOng assacialion bc:Iwc:cn cad liver oil and diabetes. Howcva-. odds ndios andlheir confidc:nce intervals an: IIIWIIly cieri. using computer packages. One that is bely available and pnwidcs lady IIDCCSS to Ihc:sc fanns or analysis is EPUNFO (http://www.cclc.gov/cpiinfal).This can be dowaloadc:cl via the intcmc:t and is in the public clamain. Man: often we ~ intcn:sted in examining dilfen:nllc:vcls of exposure. A tn:nd in odds lBlios across ditrc~ntlcyc" of expasun: proYides man: convincilll evidence of a n:IaIiaaship between the exposun: and the disc:asc: tha raul.. fIOlD the simple dichotomy of exposc:cl venus unexposed. Odds lDIios can be calculated at each level of exposun: ~ willa the bascliDc: expasun: level (usually the unexposed). A chi-square test for In:nd can be pcrfonnc:clto test for linear tn:ncI in Ihc: odds 1DIi0s.1n the thinllable then: is an appamIt In:nd with IIICR flequc:nt consumpli_ of cad
Cae r
S
I
II
Thus cadi pair contributes to one of the cells and the lOtai (r +s+ 1 +,,) is the lOtai nlBBbeI' of pails mther than the lOtai number of individual cases and conl..,1s in the study.lnten:st focuses on the pain thai ~ discordanl far exposure. lbus a comparison is made bclwec:n dDsc: pairs where the case is
exposed but the CXllllI'Ol il not and the pain where the conuol is exposed and the case is not. The odds mio is calculated as the ratio of the discordant pain :sI1. The odds ratio will themfCR be high if the pain with case exposed and conIJQl unexposed gmdIy outnumber the pain when: the control is cxposed but the casc: is noI. As an c:umplc. consider a study on hip osteaanhritil by Caopc:rel al (1998). whichexaminc:d Ihe risk USDCiated with previous hip injury to Ihc: alfec:tc:d hip (ar 10 the hip on Ihe samc: side - right or left - for the matched conllol). The data fram the lIudy are given in the fourth table The odds ratio is 46/11 =4.2.
_ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ CAUSAL EFFECT (DIRECT AND INDIRECT) case-contral studies Data from a matched casecontrol study in hip osteoarthtilis Conlrol PreriollS hip injury Pre\'iaus hip injuJy No pmrious injury
I II
NoprniolU injury
46 553
Basic analysis of malchcd studies becomes difficult in anythinl oIher than die matched pain:d analysis of a simple dichotomous exposun:.. Nowadays., matched case-conlrOl studies an:: usually analysed using CONDmoNAL LOOISTIC RECIlESSlON. This is not the same as unconditional IOlistic rq:ression mentioned above. as it takes account of the matching struClun: in the design of the study. Conditional 100islic regression enables us to lest the odds mliocak:ulated above. giving p < 0.000 1 and a 95 CJt confidence inlcrVal around the odds nttio of 22 to 8.1. This indicates thai hip injury isassociatedwilhan inm:ascdriskofhiposteoarthritis later in life. Unmatched case-conlrol studies can be analysed in most standard statistical a1IDputing pac~es. LOIistic rqression is used in many fOnDS of analysis not conftned tocase-conlrOl studies. Conditional logistic n:gression is somewhat more specialised and is nol available in all packages. It is most n:adily available in STATA for which there is a specific routine for Ihis. It can be pclfarmccl in SAS. S-plus and SPSS (sec STA11511C'AL MC'ItAOES) bul these packages Rquire use ofa PROIIORTIOIW. HAZARDS model for which the likelihood function is identical, so cannot be used quite so n:adily. EPIINFO, mentioned above, does enable much of the basic analyses and is alsoconvenienlto use ifone is examinil1l data thai an:: already tabulated (such as in a published papu). rather than the raw data on individuals. HI [See also NESTfl) CASE-C'ONI1t.OL S'IlJDJES., OBSBlVA11O.'W. sruri. IES, s,wpu SIZE DEtERMINATION IN OBSERVA11OHAL SruDIES)
Barbaae,. F.. AastID, H. ... ~ Eo E. 1993: Diet and eDdomdriai cancer: a case-coatrol study. AmmctIR Joumol of EpUlemiolo,,. 137. 393-t03. BNllow, N. E. aad Day. No Eo 19IO:-StQt&titQI methods in amcer resetm:h. \VI. I: The tmtIiysiJ of£tue-control $tlMiie.J. L)'On: Intcmalional Agency Cor Ri:scarm on Cancer. Cooper,c.,~H.,Craft,P.,Campbel"L,SmItII.G., Md.ana, M. aad COlI. . Do 1991: ladividual risk factals far hip osteoarthritis: obesity. hip injury. and ph)'sical activit)'. AmtritDII JOrmNll of EpkkD,iology 147. 516-22. ~Iut)'a, c., Coaoa, D., IDskIp, H., Lace;r, R. aad Y.... W. 1997: Aluminium coacentralions in driakin; water ad risk of Alzbeimer's disease.. Epidemiol. ogy 8. 281-6. Sc:............ J. J. 1982: Ctue-C'OfItroi sludirs. Daign. £OMUCI and DIIQ/),m. Oxford: Oxford Uai~rsity PIas. St.... L C. and Joner. G. 2003: NOIWqi_ Childhood Diabetes Study Gruup. Usc of cod liver oil during the ftrsI year of life is
lUSOCialed with lOM:r fist of cbilclhood-onset lYpe 1 diabetes: Iar;e. population-based. case-coatnJI study. NnrritYm JournoJ of Clinical Nulrilion 78. 1128-34. Tappia. D.. Brooke. H., BeDIt, R. aadGI...... A. 2002: Used imant rnauresscsad sudden infllDldcalb syndrome in Scotland: case-coatrol study. Bril;m Medit:ai JOUl'IrtII 325. 1007-12. I
categOrising continuous variables
nus is die
process of convertil1l a continuous variable such as age inlo a categorical variable with a number of categories., e.l. 'younl' «40 yean). "middle qed" (40-60 yean) and ·old· (>60). 'The practice is vel)' almmon in medical resean:h where clinicians appear to havc a lencraJ preference for categorisinl individuals (see Allman. 1991). When used 10 simplify or improve the praentation and description of the data. IfOUping individuals into Calcgories may often be useful. althoUlh the choice of category boundaries and number of categories may not be easy. When. however. the categorical variables c:n:aIecI by die process an:: used in data analysis. rather than the original continuous variables, problems arise (sec. for example. Hunler and Schmidt. 1990: Stn:incr. 20(2). Calelorisalion introduces an extreme form of measurement error: splitting a continuous wriable into categories results in lost infonnalion and an inevitable lass of power in analysis. n.c apparent simplicity of the categorical variables and the ability to use proportions and odds ratios., which an:: mon: familiar to many clinicians. are unlikely to compensate for the lost power. Retaining the continuous variable and analysing the data usina; the appropriate statistical methodolOlY will always be a far bc:uer strategy. SSE AUmaa, D. G. 1991: CllegclI'ising coalinuous variables. Brilish JoumQ/ of Cater M. 975. Haatu, J. E. aad ScIImIdt. P. L 1990: Dichaanisalion of continuous variables: the impIic:atiOlL'i for mda-analysis. JourllQ/ ofApplied P~'dology 75, .334-49. Stniner, D. L 2002: Braking up is hard 10 do: heartbreak of dichotomizing continuous dalL CQlfQt/itm JoumQ/ of PsymiDlry 47. 262-6.
causal diagram
See CAUSAL MODELS
causal effect (direct and Indirect) This ~fers to the change in outcome distribution. or some feature thermf. that would arise: under a specific intervention. It is commonly fonnaliscd using so-called countcrfaclual or potential oulcomes Y(a). which n:pn:sentthe outcome that one would possibly conlnlry 10 fad - ha~ observed for a given subject had the exposun: A been set to the value Q through some intervention or maaipulatioa. The (average) causal cITed of exposure Q on the outc:ome can then be deftned as die population-avemgcd difference E( Y(a) - Y(O). between the counterfadual outc:omes under exposure le~1 Q and some n:fcn:nce exposure level o. This is to be alntnslcd wilh die mo~ usual expected dilTen:ac:c £(t1A =a) - E
81
CAUSAL EFFECT (DIRECT AND INDIRECT) _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ __
(fIA =0). when: the expec.tc:d observed outcome Y is c0nsidered over different subpopulations defined by levels of observed expasu~ A =a aad A = o. This may not CIIIT)' the inteqRtation of a causal effi:d when the subgroups of exposed and UDCXposed subjects ~ not inherently comparable. When the outc:omc is dichotomous (with Y= I encoding "disease' and A =0 encoding "no expas~'), a causal effect can alternatively be quantiftc:d in terms of Ihe causal ~lativerisk(seeltELo\m'ERISKANDODDSRATIO),PCY(a)=
I tiP
( YeO) = 1}. the causal odds ratio (see REU.11\'E RISK AND ODDS RATIO). oddst tla)= 1t/oddst y(0)= I t. or the causal populalion attributable rraction. IP(Y= I) - PC y(0)= I WP(Y= I). nx: latter expresses by what pen:entage of diseased subjeCts the disease could have been pnwcnlcdlavoided by taking away the exposure (assuming that the exposum can only cause, but DC\'er prevent. disease). Causal effects ~ sometimes deftned within strata of given values of ~POSUI'C eovariatcs C. e.g. £e Y{a) - Y(O)ICJ. within sInIta derU1ed by the obscnoed exposure. e.g. £{ Y - y(0)1A I (in which case one ~rers to them as "causal effecls in the exposed' or "treabnenl effects among the treated'). or within so-called principal strata defined by joint counterfaclUal outcomes (Robins. 1986. Sc:ction 12.2; Fnmpkis and Rubin. 20(2). For instance. in the oontext of ranclomised experiments with lreatment noncompliance. Frangakis and Rubin (2002) rocus on Ihe local average ~alment effect (LATE) E{ Y(I) - Y(O)IA(I) = I,A(O)=OI. where y(r)aadA(r)denote the counac:rfactual outcome and R:CCived treatment under randomised assignmenl to ~almcnt r=O or 1. The LATE thus encodes the effc:a or assignment 10 Irealment 0 VCBUS I within the principal stratum {A( 1)= I, A(O)=Ot composed or subjects who would take the tn:atmcnt if assigned to it (i.e. A( 1)= I). but not otherwise (i.e. A(O) =0). By extending the previous c:onc:cpIs to a joint exposure (A. M). when:: M is a mediator or intcnncdiale variable on the causal path rrom exposum to outcome. definitions of dim:1 and indi~ causal elrects can be oonslnlcted. These express the causal errect that maniresls besides or through the change caused in that intenncdiate variable. Consider. ror instance. the Methods for Improving Reproductive Health in Arrica Trial. which investigated the effect of diaplarasm and lubricant gel use (A) in reducing inrection by HIV (Y) among susceptible women (Rosenblum et 01.• 20(9). Women received intensive ooncIom 4XM111SClling and IXOvision. aad wen:: then randomly assigned 10 either the active tmalment arm (A = I) or noI (A =0). Bc:cause them was much lower reponed use or c:ondoms (M) in the intervention arm than in the control ann. special inlen::st lies in the din:ct effect of assignment to the diaphragm ann. other tlum through its effect on condom use (Rosenblum et al.• 2009). To rormalize the aJIICept ofa direct causal etTect. define ror each subject r(o. m) to be the countcrractual outcome under
exposum level a and mediator level m. and M(o) to be Ihe counterfactual mediator under exposure level a. The controlled direct etTect or exposure level a versus refemnce exposum level O. controlling ror M. can then be defined as the expected conlnlSl Ee y(a. m) - y{O, nr)l (Robins and Greenland. 1992; Pearl. 2(01). It expresses the exposun: effect that would be realised if the mediator WC~ controlled at level III unifonnly in the population. In the example, with M expressing the pen:entage of sexual acts when: the male condom was used. E { Y( 1.0) - Y(O,O) t expresses the effecl or assignment to the diaphragm ann ifin lruth no male condoms were used. 11Iere ~ a number of limitations to the c:oncept or a controlled direct effect. in view or which altemative deftnitiom have been IXOposed. First. it is often not realistic 10 imagine rorcing the mediator to be the same for all subjeCts in the population. Second. indirect cfTecls cannot be defined in a similar manner as c:ontrolled direcl effects because it is impossible to hold a set of variables fixed. such that the elTect of exposure on outcome would circumvent the dim:t pathway.ln particular. the total causal effect. say E{ Yea) - Y{O) I. minus the controlled direct elTed. say He m) - Y(O. m)J. may not rqxesent an indirect elrect. unless the exposure and mediator have linear etTects on the oUlcome (VanderWeele and Vanstcclandt. 2009). Both Iimitalions can be oYCR:Ome by considering so-called natura) or pure direct effc:as (Robins and (in:enlaad, 1992~ Pearl. 20(1). which are de:fined as the expected contrast £t Y{o. M(O» - y(O, M(O»)J or total direct effects (Robins and Greenland. 1992), which ~ defined as £1 y(a. M(a» - Y{O. M(a» t. The natural direct effect essentially expresses what would be realised ir the exposure was administered. but its elTect on the mediator was somehow blockc:cl. In the example. H( Y( 1. M(O» - Y(O. M(O») t expresses the etTect of assignmeut to the diaphragm arm as it would ha\'C been observed ir women had not changed their rrequency or male concbn usc rollowing randomised assignmenL 11Ie difference between Ihe total causal effect and a pun: natural direct effect. £( Y(a) - Y(O») - £( Yea, M(O» - Y (O»=E{Y(a. M(o»-Y(a, M(O»J. measures an indirect effect as it expresses how much the outcome would change on average if the exposure were controlled at level a bU11he mediator ~ changed rrom level M(O) to M(a). It is termed the lotal indirect effect (Robins and On:enland. 1992). In theexamplc.E{y{I.M(l) - r(1.M(O»J would exprcss the change in HIV incidence thai would have been observed for women on the diaphragm ann ifthcy had gone back to their original use or the male condom. Likewise. the difremnce between the total etTect and the total din::ct effect gives Ihe natural indirect elTect £1 Y(o) - Y(O)l- £( Y(a) M (a»J =£t Y(O. M(a») - Y(O, M(O)t. This expresses how much the outeome would cbange on average if the exposure were controlled at level Obut the mediator ~changed rrom
yea.
yeo.
______________________________________________________________
its natwal Icvel M(O) to thc level M(a). which it would have taken at exposun: levcl a. Direct clTccts are sometimcs deftncd using concepts or principal stratiOcation (Frangakis and Rubin, 20(2); for instance. as thc exposure effect within the principal sb'alum of individuals whose mediator level was not arrectcd by the exposure. Lc. £fY(a)- y(O)IM(O)= M(a)}. Unlike the rargcoing definitions of direct cffcct. principal stndUm direct elTects do nul conccpluaiise the possibility of manipulating thc mediator. However, they havc a more limited utility because of the inability 10 ideatify which individuals faJl into which principal strata~ because the principal slnda are sparsely populatcd in many realistic applications and because thcy do nolcorrespond to a natural dcfinition ofindin:ct cffect (VaDdcrWcclc and VanSleelancb. 20(9). All foregoing causal effecl definilions require Ibe same population to be evaluated under diffcrent intervcntions! exposun:s. Because of this. they require specialised estimation techniques (see ),IAROUW. STRUCJ1JRAL !.IODFlS. INVERSE PROIWIILm" WEIOHTINO) thai work under specific ID1lcstable assumptions. such as about the exchangcabililY of subjects undcr differenl exposure Icvels (e.g. assumptions thai all conroundcn or the association between exposun: and outcome ha\'C been measured). CWl'Cnt eslimalion techniques for the causal cffc:ct £f Y(a) - Y(O)t (and likewise all other considered causal effect measun:s) infer the effcct of "noninvasb'c' intervcntions or manipulations thal allow forselling the cxposure allevel a versus o. Here. 'noninvasiyc' inlcl'ventions that set A to the value a are those that have no effect among those for whom exposun: levcl A =a was naturally obscrvc:d (VanderWcele and Vanstcelandt. 2(09). The use or counterfaclual outcomes makes dear the pn:cisc meaning of vague statements such as 'causal effect'. "direct cffect' and "indirect effect' • and makes clear. in particular. that there are different definitions of direcl effect and indirecl cffect. Whether estimates of the CXJDsidered clTc:ct measures can effectively be intelpretcd as "causal' effects in a specific application depeads on whether the required unlcstable exchangeability assumptions are mel Sv. EG Fa........ C. ud RabID, 0. 2002: Principal stnlificalioa in c..sal infe.-:ncc. Biometria 58, 21-9. Pearl, J. 2001: Dinxl and iadiRct effects. In Pr«m/illgJ of tire Semrtl.Ynth CDII/tmfte Oil Uncertaint)' tmtl artijicial iRtelligencr. San Francisco: Morgan Kaufmann.. pp.4II-20. RabIDs, J.1\1. 1986: A new IJIIIIIOICh to c.asaI infe~nce in mortality studies with sustained exposure periods - application to control of the bcaJthy 'A'om survivor eff'ecL MatMnlDt;cal Modelling 7, 1393-512. RoIIIaI, J. PtL ad One........, S. 1992: Identifiability and ellChan,eability for direct and indiRct dfects. Epidemiolog:t'l. 143-55. RaIeDbIaJD. 1\1., Jewell. N. p.. taD del'
s..
....... 1\1., SIIIbcUI, Va Ow Strate... A. aDd PIIcIIan. N. 2009: Analysing dinxt effects in randomized Iriais with secondary intcn'allions: an appliC4lion to buman immunodeficiency vinas preveation trials. JOIImaJ of the Ro),al Statislital Sot:iel.' - Series
CA~ITY
C 172. 443-65. VuderW.... T. J. ad V......1udf, S. 2009: Concct*Jal issues concerning mediation. intavcntions and composilioL StaliJtks and ilJ inter/acr. 2, 457468.
causality Thc two fundamental principles for establishing evidence for a cause and effect n:lationship are deduction and induction. 'I1Ic flJSt. with its roots in carly Greek
philosophy. encompasses malbcmatical reasoning: starting with a pn:mise fannulated withoul reference to the outside world. a general Ibeory is developed through logical reasoning and subsequently confirmed by statistical obSCIWlion. Induction. contrariwise. aims to establish a general principlc by observation of the natural world and sceJc.s 10 conOnn Ibis principle tJuuugh prediction and further observation. In contrast to deductive reasoning, inductivc reasoning proceeds from the particular 10 the general. While there can be no doubt that much of modem scicnce strives to make progress through inductive methods. the dcductb'c principle has a firmer pounding in logic. As Hume pointed out. simply obscning that one event foUows another. no matter how many times it occurs, does not establish Ibalone evenl caused the oIhcr. 1hc concept of whal a cause is needs to be set in context with the knowledge or Ibe time. In 185S John Snow established the link between a "morbid matter' carried in waler and acute. often fatal. dianhoca in London (Snow. 18SS). Snow'S evidence consisted of temporal statistical associations. geographical associations in relation to the water companies supplying the city and consideration or a plausible roule of infection through ingestion or drinking water. It was the assembly of these various strands of evidence Ibat led 10 the premise that the water soun::e caused the dianhoca and a subsequent outbreak in Central London gave Snow the chance to cstablish deductiYC proof. by removing the Broad Streel watcr pump. with the immediate effect of stopping the epidemiC (see IDSTORY a; MEDIC'AL STA11STICS). Snow postulated a cause of c:holeru 30 yean before the bactcrium was isolated. As scicnce delves deeper into genetic and molc:cular mechanisms. we alter our level of definition or causal radors. In realilY. few causc-effect associations are simple tworactor problems. Many or our prominent chronic diseases are multifaclorial in nature and many of the factors chat contribute to causation are yet lo be discovered. Despile Snow's example. much scientific work progresses withoul deductive proof: empirical knowledge seems 10 accumulate through methods that may lend support to but do not actually guarantee COI1'CCt conclusions. Statistical procedures are employed in obscrwtional sciences. when: a hast of unknown sources of error. including ME.o\SUREMENT ERROR and random ftuctuations, musl be considered berOR even progressing towards consideration of causality. Formal 'proof" is genemlly not alIainable in observational sciences and il may be fruitless 10 try 10 demonstrate causality in 63
CA~MODas
________________________________________________________
a fannal way. Mon: often- a number of usociations must be considcn:d together to assemble the totality of evicleace. The BRADRIlD Hill. CItrI"EIUA offer guideliDes for consiclc:riag the talalily or e\'idcna:. Some of these criteriL such as establishing temporalily and demonslnlling n:venibilily. ~ powerfullaols in determining causalily, whcmls othcJs may depend on specific cimanslDDccs. Bradford Hil)"s aim was primarily ID provide a mon: SlrUctun:d appmaeh ID infarmilll dc:cisiDns for IRvenli~ action. OIhcr wrilers ba~ advocalc:d decisions based on Popper·s concepl or n:fillDIion. Rcfutalionists would sugest thai sciena: can advance mo~ rapidly by formulDling radical hypolhcscs and disauding cnvneous theories ahan it can by liuidcss accumulation of suppodinl evidence. We could make many stalcmcnts in faWKll" of a hypDlhcsis and still fBi11D establish il. but we could lake JUSI one cumple thai disproves the hypothesis IDCIOIICludc il is false (e.g.. one black swan is proof against the assertion thai all swans ~ white). Howe~. even the process of Rfulalion dc:pcnds on observalion and is Ihcn:fon: ilsclf IIDl devoid of uncenainly. Thc~ n:mains a crucial role fOl' stalistics in any science basc:d on obsc:mdion: to set probabilistic limils on whc:lhcr an observed association exisls or shauld be ipon:d. Many widcJy accepted stalisticaJ practices appear to ~ to clccluctivc 19SIDIIiDI. 'I1Ic NULL HYPOnIESIS is a Slalcmcnt formullllCcl prior 10 any knowledge of the daIa and then:fon: a lest or the null is an inference from the hypothetical general population ID the sample: "Jf then: is no association in the lcaera) population a Rsultlike the one seen in the sample would ha~ probabilit)' P: In Ihe UXElJIIOOD approach to estimation, computations proceed ftom consideration ortlle hypathclical value for the parameter to support for ahat value in the particular daIa obscnal. Howe~. fn:qucntist theory would appear to be embcddccl in inducti~ n:DSODing: we imqine an experiment rc:pcating an infinite manbcr of times. under the assumption that given enoup n:pelilions we will ullimalcly arrive alb wth. While this n:asoning secms Iopcal if conditions remain unalten:d.. some would arsue thai ifconditions an: likel), Iochange in different populations or under the inftuence of additional variables. then a gc:aeral principle cannal be asscrlc:d on dais basis. As with anydisciplinc..ourability todelc:nnine meDnilllful n:sulls in slDlislicai analysis dc:pcnds on the appruacb we adopt. The disco\ocr)' of a slalistically significanl raull is paunds forn:jc:c:ling a null hypathcsis. but is notevident'C for a previously unfonnulalc:d hypothc:sis on the st~ngth of the currenl data. Hence. dn:dginl clata for significant Rsolls takes us no ~ to establishing causality and will at best mise possibilities for futUM invcstiplion. Likewise. ilwe ~ seekinl "explanation· in a statistical model. the decision to include a term in the model. guided only by considcndions of stalislical signiftcance (refutation of the null). would IIDl n:spccl deductive principles (Maclure. 1915). If scientific
explanalion n:lies on testing specified prior hypathcses. a mon: consistenl modelling approach would be 10 include modellenns. even if Ihcy ~ nul signincant in the curn:nl JGW data. For fUrther dewls sec Weed (1986). MacIaN, M. 1985: PappcriIIn ~fUlation in epidemioloJy. Ammnm JOIII1ItlI of Epitkmiology 121.343. SDDW'.J. 1855: Or lire"",. of t..",,'lIIIrcstiDlr of ('lroIml. 2nd edition. LoncIan: Chun:hill. W.... D. L 1986: On die logic of eausaI infemacc.. A.,i"", JourllQl of Epitkrnlology 123.965-19.
causa. models Thc:sc models attempt
to discover
whether an observed aSSDCiDlion between an expnsun: (e.l. cipn:Uc smoking) and an oulcome (e.g. high blood pn:ssun:) arises because the exposun: causes the disease or whether it is a SPUT;"'" MlOcitlliOtr. A spurious assacialion can arise if boIh the ex)JOSlR and the disease have one (or mon:)cammon cause -e.g. if socioeconomic stalUs is a cause of both hia;h blood pn:ssun: and cigamte smoking. Tbcn: arc four major types of causal model (see On:c:aland and Bnonbaclt. 20(2) and many definitions of 'causal' in an epidemiological CXJIIICXt (sec Panuc:andoJa and Wccd. 2001). One lype of causal model is the ctlratli tiillgnm. (Gn:enJancl and Bnunback, 2002; HcI'lUlD el til.• 2002). Such diagnuns link exPOSUR. outcome and oIher variables by arrows n:pn:sc:ating din:cl causal effects. A hypothetical example for smoking and hilh bload presson: is shown in the finI figun:.
cauaa. models causal diag18m showing a possible relationship between smoking, high bloodpressure and
socioeconomic status Such diagrams can be drawn rnm prior knowledge of causal mechanisms. Uses include deciding whether adjusting for CXJIIfounding wriables would incRasc or dccn:ase bias. For example. from the filOn:. one would adjUSI for socioeconomic status in analysing the relationship between smoking and hilh blood JRSsun: (as it is a common cause). (For IlIOn: details. sec Heman. el tiL. 2OD2.) A second type 01 causal mocIcl.1he collnlerftldUtlI model. arises from a definilion of CAUSALITY: "Exposure makes a difference in joulComc (or Ihe probabilily of an outcome) when it is pn:scnl. c:ompan:d with when it is absent" (PamscandoJa and Weed. 2(01). Thus the ·coUDterfactuaJ· arises because the dcfinition hypothesises about what ·mia;ht have been· if conditions had been other than those actually o~ served (Maldonado and Gn:cnland. 20(2). 'The deftnition also specifics that all oIher conditions should ha~ Rmained
_ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ CAUSE-8PECIFICDEATH RATE
i.e. it is only the cxposlR that WII5 (hypothetically) changed. For example. wc c:auld say that smokilll causes high blood pn::ssun:: if blood )R5MR is higherwllc:n a penon smalcs comparailo what it would be if that same penon we~ a DOIISmoker. nte causal effect of smaldDl on blood prasun: for an individual c:auld then be estimated by the diffcn:ac:c between their blood pn:ssun: when they s....cd ancItheirbloocl pJaSlIM iflhey did not smoke. However. only one or Ihese outcomes for eacb person is actually observed. 1'1Ic unobserved quantities an: estimlllCd using subslilUlcs (Maldonado and Greenland, 2002). This could be by using uaexpased individuals 10 estimlllC the oulc:omes if exposed individuals had in fact been unexposed (OR:enland and Brumback. 2(02) ar by imputiDlIhe outcome from observed covarialcs. In a nmdomised mal, we assume that In:alment ancIcontrol pvups an: balancc:cl in all n:spec:ts. cXccpllhlllthe cxpasun: and then:fom the outcome in the expasc:d poup can be used as a substitute far the: outcome in the cannl gmup wen:: it to ha~ bcc:n exposed (Mandolado and Gn=enland,2OO2). 'l11c third type of causal macIcJ elisaaccl in the 2Q02 n:view. the: sujJicienl-colllponenl t:tlUN macIcJ. assumes that the: autcane is aused by sevcnd causes. none of which is ncccssauy and l1IfIk:icnl alone to cause the disease (Gla:nlancl and Brumbac:~ 20(2). Such maclcls me often IIIown as PIE CIWO'S. with cac:b slice IqRSI:nting one of the components or the overall cause. Forcxamplc. high blood pn:ssun: couldbec:aused by the piaCDCe of any 1\\'0 of smokilil. low soc:iocconomic sIatus and beilll CM:IWCight (see the second Iipn:). One elisadvan. .c or such models is thai in cxdcr to explain n:lationsbips such as Ihat of smoking with lung cancer. it is necessary to assume that ";smoking is one elemenl in a sufficient cause and thalthe GIber clemen.. simply ha~ not been identified ycf (Parascandola and Weed. 2001). 11ris is clearly a slnmJ assumptiDD to maIcc in many an:as of medical stalistic:L The fourth type or causal mocIcl.lhe STRurnJRAL EQUATION MODEL. may be thought of 115 a paramclerisation oflhe causal graph (Greenland and Brumback. 2002). Hen:. each n::lalionship DD the graph is expn:ssed 115 an equation. with each yariableoccurring as an autcomc: in only oneoflhe equations. All paramc:IeIS ~eslimaled simultaneously and can include CIIDI" Ienns and underlyinglREHf VARIABLES (as unobserved variables) and ClDll'Clation between any of the variables. Si..p-Manoux. Richards and Mannot (2003) usc:cl causal cliqramsand slructuralequation models to analylie the causal n:Iationsbip between leisun: actiYities and cOJniti~ funclion. 1he causal diapana showed eight measured variablcs (including the outcome) and seven unobserved variablc:s. and included cOl'l'CJation between leisllM activities enlailiDllow and high CVJniti~ elrod. Participation in leisun:: aclivilic:s. particularly social ar hip cognitive effort ac:livities. was positively associalc:d with cOlftili~ function. KT CODSIaDI;
causal models Sulficient-oomponent cause model showing hypothetical causes of high blood pressure 0 ........... S. aM • .,.....,.. B. 2002: An overview of ~Ialialls IIDGIIg causal modeUiag medIods. Inlf!t'llQlitmtll JDUl'flQI t1/£pillemiolo.o'JI.I030-7.aen.a,M.A.. H............. s., W....., M.M. ... Mltdaell.A. A. 2002:0nasaI bowled&c as a pcmquisi1c far oonfouading evalualiaa: an applicatiOll to birth defCClS cpidemioloo. NlMnCYIII JtJllTllQl of Epitltmiology 1.5.5. 17~. MaIdD....., G. ad Oneallad, S. 2002: Estimating c.asaI effects. Inlmtllliolltl/ JOUI1ItlI of Epitlml-.o' 31. 422-9• .,........... Me ..... Weed, 0. L. 2001: CausaIioa in cpidcmiolol)'. JtJllrlllllof EpitkmIoIogy _ Communil), HeflII" SS. 9OS-12. SI~ A.. ~ l\L ... r.1mnof, M. 2003: i.eislR actiYilies aad cognitive fuaclion in middle age: evidence fIan Ibe WhiteW11I study. JOUIIIQI ofEpidemiology GIld OInt"".,il>, Heflll" S7. 907-13.
e_u.. epeclflc death rate
11Iis is • death rate calculated far pc:opIe dying fRJIR a particular disease. AlI-c:ause monaJity ndc:s pmvide a summary of the overall moltality of a population. bulthe distribution of causes of death can vary considerably between populations. Classically. mortuly fRJIR infectious diseases is higher in counIries thai ~ less deyeloped. when::as diseases thal ~ chronic:. and primarily decl the elderly. pn:dominale in thc dew:lopcd world. In saudying a population's mDItaIityexperiencc. it is thc:n:fon: necessary to co.-... the specific causes of death rather than simply the all-cause death rate. the table gives the cause-specific: rates for a variety of diseases for eliffcn:nl c:auntries. nte rates ~ calc:ulated by dividing the number of dcalhs from the cause in question during the year by an estimate of thc mid-year population. Thus. the Romanian rate for tubm:ulosis is derived from 2130 (the deaths from tuberculosis occurring in the yC8l' 2000). elivided by 22.435.000 (the number in Ihe population far that year). nte n:sull is then multiplicd by 100.000 10 giyC the rate of 9.5 per 100.000 population. 8&
CENSORED OBSERVATIONS cauae-speclllc death nate cause-specific death rates per 100 000 from selected causes from various countries (United Nations, 2002) CDUlllry ArgCllliDa (l996) Aumalia (1999)
Bahamas (l997) JIpIII (1999)
PImama (1997) Ramlllia (2000) South Mica (l99S) United Kin""" (1999) Unital SlIdeS (l99B)
TIIbe,t:IIlosu 29.5 0.2 0.7 2.1 4.1 9.5 32.2 0.9 0.5
HIVI AIDS
Lun,
Cardiol'tUCllltlr
Acc;dmls turd
All
CllllceI'
dUmse
"iDlerrce
ctIU:WS
52.2 21.9 28.8 29.7 56.9 64.2 119.4 33.4 55.6
863.9 337.9 26t.1 740.1 418.7 1140.3 Ci06.2 1062.3 163.9
23.2 0.4 50.2 0.0 15.6 2.2 13.2 0.3
5.0
The lable sIIows that &"Ciden15 ad violence ~ hi&h in South Africa. wllcn:as canliowsculardiscase is of conc:ern iD Romania. It mull be noled thai Ihcsc an: crude rates and tile difren:al age struct1R5 of Ihc: populalions have DDt been CllDSicielai; lheeamparisons CD thedeR be mislcadinl (sec /tOE-SPECIFIC RATES).
Cause.-specifie death I'IIlesan: publisbccl by manycaunbic:s andona. an: pn:scntccI asap-and scx.-spcc:iftc ndcs I"oreach causc. The rates ~ pracntc:cl by cause of'death as classified by tile International Classifieati_ of Diseases (World Health Or&anisation. 1992). Replarupdates to Ihc classification an: n:quilai 10 accaunt for Ihc: chanlil1l dcftnitioas of disease and. in particular, to n:cognise new diseascs. IW example. acquilai immunodeficiency syndrome (AIDS) did DOl featun: in the 9th ~vision but has been included in the 10th. For analysis of disease time bends. ·bridpns· amJIS tile ~vi lions can pracnt some difficulties due 10 tile chaftlinl definitions. CMse.-specific rates can also be obtained far new cases of specific diseascs. MDY countries now have cancer n:gislric:s that publish national ancIIor n:ci-al clIDCCr incidenc:e niles. These an: collated internationally by the IntematioDal Alenc)' ror Resean:h (Parlin ellll. 2003). which publishes qe.ancIsex-specific incidenc:e rates for various types or cancer fiom mIlD)' caunlric:s 8CIOSS the world. Similarly. I'IIleS for tm:r200condilioas"ve been compiled by tile World Health HI Orsanisalion (Murray and Lopez. 1996). Marray. c. J. L - ' Lapn, A. 0. 1996: GIobaI_IIII sialiJlic£ A t.YIIIIplntliltm of ;"dMIK'l'. prnIIleII« _ morlality ~stimtll~s for Drt!f' 200 ctIIIIliliDlu. Han'lnl: Wortd Heal... OrpnisatiaL I'IItda, .... ww. s., ,....,. J.. ......... L .... 'I1IoIuI, D. B. 2003: CtlllftrirrtitleMrinJlWftIHIlirwnts, Vol. VID. L)'OD:!ARC Scicalific PUblic.iaas. U...... ~ 2002: 2000 Demo"aplJic ~Ic. New Yok United NIIIions. W.... IInUb 0rpaIIa.... 1992: Inl'l7ffIliMtII sialuliCYlicltmi./i«lliDII ofdisease,. RIfIlftiII,lIllh
pl'Dbkms. 10lh rmsiaa. Gcaew: \\aid Health OrpniSldian.
17.9 3.6 20.6 6.0 37.9 9.7 58.3 51.1
297.3 135.2 11.9 122.2 118.3 701.9 103.6 426.2 349.3
censored ob8erVlltlona This is a distinsuishil1l c"ractcrislic: of timc-to-eftnt data (sec SU1lVIVAL ANALYSIs). Censored obsc:nations CCllltain onl), paIIiaIl)' abscrved infOllDlllion about the time to Ibe evcDtofinlCraI; i.e. the exact time oflhc ew:nt is unknown as it may DDt yet"ve occum:d or be known to haftoccum:d.lWexampie. in a study of time to recum:nc:e of a parlic:uIar medical condition. say leukaemia afta' ·succcssf'ul· bone mallOW IransplanlaliOD. some: patients ma)' not expc:rience a m:urn:acc at the end of Ibe lIudy. some may dnJp out or be 105110 follow-up. some may expc:rience tile ew:nt of iDterat duriDI successive medical visils, while )'et othc:n may experience a ·compc:lins' event. say death. which prevealS further follow-up of these subjeclL There an: difl'en:at fonns of eensoriDg. The most cammon in mc:dicalsluclic:s is ,ighl «IUD,lng. This oceun when b)' the end ofa subject's follow-up the e'Vent ofinten:sl has not been obscm:d. In this situalion all that is known is that the true unobserved ·surviyal' lime cx.cc:als the observed ceRSOI'Cd lime. Most of the examples aln:ady seen ~ or this form.
lift cellMN'In, occan when the true surviyal time or a subject is less thaa Ihe actual lime observed. For cx.ampie. in tile Ic:ubemia study jusl examined. subjects may relapse before "eir finI medical visit. 111us. onI)' Ihe inaJlllPlete information thai the true m:ummce times ~ less than the limes 10 their first IDCdical 'Visit is awilable. 8aIh forms of cellSDl'inl an: special cases of Inler,.,,1 cel&SDrilrg. when: a subjc:cl is kaown only to ha~ experienced tile event within a specific time intc:rval. F'urlhcrmcR. Ihc censorinl mechanism CD be independent or dependent. In the fanner, Ihe true lUn'ivai lime or a subject. whose observation has bee. eenllRCl. is independent of Ihe mcchDDism that lxaqhl about this censoring. Allemalimy, Ibe survival pnISpCCIs for a homopneous Croup of subjects ~ tile same in Ihose c:ensored and in those continued to be followed up. Dependent censorinl CaD occur when subjects an: wilhclrawn 110m a stud)' beeMse of their
_ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ CHI-saUARETEST ~nt high or low risk ofexperiencing the event. This type of censoring makes saandard sUl"Yival analysis techniques invalid. Thus it is important when cc:asoring CJC:lCU15 toc:ollcct as much inronnation as possible on those subjcds with cel1SDl'ed obscl\'alions. in order to decide whether the mechanisms behind the censoring types eDCountemi arc independent or dependent. Censoring should nul be "ignon:d' as valuable information is contained in dlosc subjects withcensorcdtimes.1'hcrefore. any analysis performed must take account of ceasoring to make valid inferences.. For further details see Collett
(2003).
BT
CoIeU. Do 2003: Modelling sun'irai dota in medical ~S'I!tI1'fh. 2nd edition. Loadoa: Cllapman tot HalIICRC.
central limn theorem
See NORMAL DIS'I1UIU1ION
Central Ollice for Research Ethics (COREe) See ETHICAL REVIEW COMMl11EES
chI-square dlstrtbutlon '111is is the PIIOBABJUfY IXS. TRlBtmON of the sum of the squares of independent normally distributed random variables (denoted X2 and sometimes refem:d to as chi-squared). If we have a wriable. XI' that has a NalMAL DlmtlBUTION with &IEAN 0 and VARIANCE 1, then the sqUll'e of XI will have a chi-square dililribulion with one DEGREE OF fREEDOM. often denoted X2( 1) or xi depending on the text. Similarly. if we have n independent observations. each from a nonnal dislribution with mean 0 and variance I. say Xl, X2• •••• X". then the sum + Xl + ... + will have a chi-squan: distribution with ndegrusoffRCdom. here denoted The chi-squan: dislribution can arise from many other cireumstances. but this definition makes it clear thai since it is the distribution of a sum of squaml numbers. the distribution's delUiily function can only be positive for nonnegative numbers. It can also be seen that a variable taking a chi-square distribution with. for example. scven dec;m:s of freedom is the sum of seven inclepcndent variables each with a xi distribution. Since the xi dislribulion has a mean of I and variance of 2. this result tells us that the distribution will have a mean of n and ~ancc of 2n. In addition to thesc relaiionships. we noIc thai the distribution is identical to the EXPONEK11AL DISTRIBUTION with parametcr O.S and thll, in gcncml. the X; dislribution is identical to the OA!.BIA DISTRIB~. with panuncters nil and 2. As n becomes large, the distribution is bc:ucr approximated by Dnormal distribution (with mean n and variance 2n). It has a sJilhtly more complicated relationship with the F-DlmtlBU11ON. for which it is the limiting dislribution after scaling..
x;
xi
X;.
xi
xi
x!
'I1Ic shapes that the distribution can take and some of these relationships are iIlustnted in the ftgure (see page 68). For further details of the n:latiolUihips with other distributions, see Lccmis (1986). As can be seen. with one or two degn:es of freedom the made of the density function is at zero Dnd is strictly decreasing with the value of the madam variable. With more delJ'CCS of fn:cdom. the density function takes the 'whalc' shape. which is morc usually associated with the chi-square distribution. 'I1ac chi-square dislribution is most obviously used in the an-SQUARE TEST, but also appears whca testing hypotheses about variances. when pcd'onning LlKElJHOOD RAm tests and in some NONPAJl,UIEJ'RIC METHODS (e.g. the KRuSICALWALlIS lEsT).
Here the central chi-square dislribution has been discussed. There is also a non-cc:alral chi-squan: dililribution that arises when the normal random variables that define the distribution havc a nonZCIO mean. For further details sec Altman (1991). AGL AItmaD, 0. O. 1991: Practical slatistics/Dr Dltdkafreseardl. Boca Raton: CRe PrcssfCllapman tot Hall. ........, L M. 1986: Rclalionships llnOIlI oonunon uDiwriaIc distributions. TIw Amtriam Slatistician 40. 2. 143-6.
chi-square teat This is a statistical significance test used to assess a variety of hypotheses of categorical data. particularly when interest cc:atres on the distribution or obscrvalions across catcgories.. For example. a study might record the ethnic group of individuals and interest might cc:a~ on the plOportion of individuals in each ethnic group. .Categorical dala an: often pmiCllted in FREQUfNCY T.o\BLES (or CON11NOENCY TABUS). where cadi ccll or the table shows the number of observations (counts) for a particular combination of categories for the variables of interest. Chi-squan: tests are a form or HYFOTHESIS lEST w~ the hypothesis speciftes the expected distribution of observations across the cells of Ihc frequency table (the expected numbel' of individuals in each cell). The chi-square test statistic, %2. pIOvides a measure of how much the counts n:cordcd in the study (the ·obsen'ed COWlIS') deviate from counts pmlicled by the hypothesis (the ·cxpected counts'). A small "-VALUE is evidence that the hypothesis is false. (The formula for the chi-square test statistic is given in the c:alr)' for COK11NCJENCY TABLES.)
Frcc:man et al. (2002) provide an exampleoflhe usc ofchisquare tests. This re-audit of hip fracbR in Easl Anglia involved seven hospitals and analyses were pcd'anneci to establish whether there were any difrerenccs between hospitals in terms of patient demographics. One of the variables tested was patic:at gender. In this case. the hypothesis to test was thai the distribution of patienls across male and femalc calc:gories was the same at aD of the hospilals. In other words.
S7
CHI-SQUARE.TEST _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ __ (8)
(b)
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i
i
i
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10200
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ch......ie.dlstllbUtloli Ib'rslintl the form of the chi-squat8 pmbabllly denslty'function and its I81aI/onshf1s wIIh other disIribuIlDns: (a) chi-square tlslrlbution wiIh one degree of freedom; (b) the F-clsflfbulion with one and one thousand degrees offfeedom; (c) chi-squtue disttibution with fwo degtees 01 freedom (equivalently the exponential dsItIbuIiDn with a PfllllmeterofO.5); lei) c/JI-squal8d1f11dbu11on wllhsbc degreesofffflfKlom; {eJchi-squatedistdbution with ten thousand degtees of freedom; (I) nonnaI distribution with miJan of ten f!Jousand and WIIia~ 01 ~ty thousand Ihe hypothesiS was that the pmpaiti_ofhip fracture pallenls who WCR maJewas the same at aU ofthehaspitals. 1herauJt chi-square tell was =1.50 and P=o.48. indic8ling that Ihem.wu·lIOC\'ideaceofadillerence betweea hospitals the piapodion or hip IiaC:tun: patients who were male..
ora
r
in
TbeJe. are lIRe lest: die .common . types of chi-lqUIR . ror iDdcpeadencc aad the test rew homogeneity. 11Ie chi-squam .ootine.u-of-ftl lCSI is appropriale when Lhere is a single group of subjeclS and a sinJle wriable of
goodness-of-ftt tell. the ICSl
_________________________________________________________
interest. The hypothesis in this sort of test specifies a precise ubibution of SUbjcclS across calcgorics. Few example. this test could be used to ddennine whc:thcr the ethnic mix of a patient group from a study is dill'erent from the (known) ethnic mix in the general papulation. The chi-squan: lest for independence is appropriale when there is a sin;le group of subjects and two variables of interest. In this case. the hypothesis is that the disbibution ohubjc:cts across calcgories in one variable is the same for (i. e. independent of) the categories of the other variable. For example. this test could be used to detennine whClher the incidCDCIC of a disease is ~Iated to the ethnic mix of a patient group - in other words. whether the propoItion of patients with a disease is the same for all ethnic groups. The chi-sq~ test far homogeneity is approprialc when there are sc,,,ral groups of subjcclS and a sin;le variable or int~. This test is used to dc:tcnninc whClher the distribution of a variable across categories is the same for all groups. The study by Fn:cman el 01. (2002) provides an example of this salt of test whe~ the groups ~ hospitals and intcn:st cen~s on whether the distribution of male and female paticnts is the same at all hospitals. Each of these tests is only appropriate when then:: is no nalUral ordering to the calegories(i.c.thedata~ nominal). If thecaICgories~ordcrcd(i.c. theclalaare ordinal). e.g. when the variable of intm::st is • group. then other analyses should be usc:cL such as the chi-sq~ test for tn:nd (see. for example, Altman. 1991). The chi-square test is a parametric test: it is only a valid test when the expected number of observations in each cell is not too small. (A rough rule of thumb is that the expected number of observations in each cell should be at least S. However, a less stringent crilcrion is commonly used and has been shown to yield satisfactory ~ults: namely no m~ than 25 4Jt or cells should have an expected cell count of less than S. proVided none is less than I.) The test can bceomc invalid when the expected number or observations in a cell is \'CI'Y small anellor when the total number of observations is small. In such cues it can be prudent to usc a continuity correction (see YAlES' CORRECrlON) or, even better. employ a NONJWto\. !.tETR1C' or EXACT).IE11IOI) alternative (e.g. FISHER'S EXACT lEST). The samplin; method should be considered when determining. what sort of chi-square test to usc. It is only valid to test a hypothesis thai makes sense in ~Iation to the way in which the data ~ gathered. In the hospital example. ~ ~ several independent groups of patients (from the seven hospitals) and a single variable of inte~st (gender). In this case, il is valid to pclfOnD a lest for homogeneity. but it is not valid 10 perform a test for independence. Chi-squan: tests only proVide an overall test of a hypothesis. If a chi-square lest is significant. it may be nccessary to perform funher post hoc tests in order to detennine in mo~ detail wbc~ significant deviations from the hypothesis exist.
CUN~AL1R~LS
In the example from Freeman el 01. (2002). had the tesl been significant. this would have indicalcd that the proportion of hip f'ractu~ patients who we~ male was no/the same at all of the hospitals in the audit. This does not specify precisely those hospitals that wen: significantly ditTen:nt flUlll each other. In this case. a I-tesl of the difre~nce between proporlions far each pair of hospitals could be used. but it should be noted that such post hoc tests would be subject to the usual problems of mulliple comparisons (see MULDPLE COr.lPAJlIS(»l FROCEDURES).
When a wriable has only lwo categories. e.g. geneler. the data may be analysed in lenns of proportions rather than fn:quencies. This sihlatioa may be analysed using logistic regression. which allows mo~ complex hypotheses to be tested. An allcmativc and mo~ ftcxible analysis for any number of variables with any number ofcategories is fOlSSON REGRESSION.
Chi-sqU8l'e teslS ~ described in mast introductory statistics texts (e.g, Altman. 1991: Wild and Seber, 2000; Ag~ti. 20(2). PM A.,.u,A. 2002: CtJl~gorit:tlltlola IUlQlysis. 2ndeditiOll. New York: John Wiley & Sons. Inc. AI""... D. G. 1991: Pr«timl slatiJlies/1H' metlicvl "search. London: Chapman & Hall. Free....... C.. Todd. C.. CamIlleri-Female. c.~ I·"~ Co, 1\1I111'III. P., Palmer. c. It., hrbr, M., P.,.., B. aDd Ruslltea, N. 2002: Quality impnwomenl for patienls with hip fract&R: experience from a multi-silc audit Qualil,. alfllSafety in Healtb Care 11.3.239-45. WIld. c. J. IIDII Seber~ G. A. 2000: Chanty mCDUtllers: a jIr" COUI'Je in tlola QIIIllysiJ and inj'ermce, New Yort: John Wiley & SoDs. Inc.
chi-square test for trend Sec CASE-coNrROL SltJDlES Christmas tree adjustment See INTERIM ANALYSIS classlflcaUon and regression trees (CART) See 11lEE-S11WCTUJlED ME1HOOS
classification function See
DISC'RWJNo\NT RJNC'I1ON
ANALYSIS
clinical equipoise Sec E11IICS .o\ND CLINICAl. TRL\LS clinical trial protocols See
JIROfOC'OLS lOR CLINICAL
TRIALS
clinical trials Also known as randomised controlled llials (RCTs). these ~ studies of a medical intervention in which the allacation of patients to the various experimental groups. at least one or which is a control group. occurs by an a/eolor),. or chance. mechanism. Such a study has a number of essential fealu~s in ackIition to randomisation. It is hypoihesis-clriven with an unambiguous ENDPOINT assessed in a way that assures unbiased measurement; it has secvndary 69
CUNI~TR~
_________________________________________________________
endpoints that add cn:dibilily and inlclpretability 10 the primary outcome: it defines its study group in a way that allows logical inference to some defiDllble popuIalion: it uses an ethically and scientifically defensible control group: and a clearly wriuen protocol gemas its pnx:cdun:s. Because the experimental units an: humans. these trials requin: a rormal process of informed consent as well as assurance that the safety or the participants is monitored durinl the COW'se of the study. Randomisecl controlled IriaIs may enrol tens. huncln:ds or even thousands of participants. While the general structun: of the design or such a trial is independent of its size. the number of participants enrolled aft"ects many aspc:clS of the conduct of a trial. Small sinlle-centn: trials tend to collc:ct a lal of data. Multicenln: trials typically collecl somewhat fewer data on each palienl. Withe methods orcolleclion tend to be highly Slructun:d to ensun: axnparabiUty across centn:s. A so-called 'larle simple trial' n:cruits thousands or people and collects a parsimonious amount ofdaladirectcd at a few pointed questions (Vusuf. Collins and Peto. 1984). A classification of trials of elmls or biologics relevant in the regulatory sc:tIiRi categorises them KCORlinl to their phase. PHASE l11UAlS. the first trials of the product in humans. aim to gain a preliminary understanding of the safety of the product and to select doses far further study. PHAsE 1I1RL\LS define the dose more pn:cisely and perhaps collect daIa germane to a prelimiDar)' glimpse at el1icacy. often thmup the use of SUftOIIIle endpoints or biologic mukcrs. In many therapeutic an:as. Phase J and U trials an: Dol nandomisecl. and sometimes not controlled. because their goals can be achieved with Simpler designs. Confirmatory. ar PHAsE W "I'IlIAU aim to test the emcacy of the product. 1)pically. a Phase III trial is randomiscd. Trials pcrfarmcd after the product has bc:cn approved for licensing. whether they an: randomisecl or noI. an: somelimcscallcd PHAsE IV 11lW.S. This section toucia on the early history of the modem mncIomiscd controlled trial. discusses its salient features and describes some or its limitalions. Sevcraltextbooks proVide thoraugh intnxluctiaa to these trials (Pocock. 1997: Fric:cIman. Furbc:rg and DcMeIs. 1991: Meinert. 1998). The earliest modem randamiscd clinical trial studied streptomydn. the first truly ldive drq for the trealment of tuberculosis. Stn:ptomycin. discoven:d in 1944. had shown very promising. raults in unconlnJlled pilot studies in the USA. At the end ofthe Second World War. limited supplies of theelmg wen: made available in On:at Britain forclinical usc. Because of the beJief that the drq had promiSing therapeutic aclivity. a portion or the available supply was n:servcd for patients with the two most lethal rorms of tuberculosis meningeal and miliary disease. The rat could be used ror the large majority ofpalicnls. who had pulmaDlU")' disease. Since it was manifestly impossible to lmlI everyone with pulmonary tubemllosis. the Medical Research Council decided that
the best usc of the small amount available would be to study its effects in a conuolled setliRi. The study that followed (Marshall ~, aLe 1941) was a mullicentn: conlavllc:d trial compariq stn:plomycin to standard bed resL Random numbers plac:cd in sealc:cl envclapcs governcd the trealmc:nt assignment of the 109 palientsentcml. Patients wen: eligible if they had 'acute propasive bilateral pullllDDar)' tuberculosis or presumably recent origin. bacteriologically proved. unsuilable for collapse therapy. age group IS to 25 (1IIler extended to 30)'. The narrow age poup was chosen to limit the number of eligible patients. Physicians raponsible ror evalualing. radiological change with tn:atment WC~ unaware of the batment assignment. Results showed a clear benefit of stn:ptomycin: the publishc:cl n:porl rerc:n to a few or the observed tn:atment ditren:nces as "stalistically sipilicanf. lWo anonymous editorials accompanied the publication oflhis trial. One dealt with the implications of the n:sults ror tubcn:ulosis therapy. The second. entitled 'The controlled therapeutic trial' (Anon. 1941). COIIUIICntcd on the nateworlhy aspectsoflhis study. including the precise definilion of the patient population. the advantages of multiccntn: collaboration to assun: adequate numbers of study subjccls. the need for screening palential subjects so that they conrormed to the elilibility requirements and the wac of the "ingenious system or scaled envelopes' to ensun: that aclwnc:cd knowledge of the tn:atmcnt assignment would DOl inftuence the decision about patient elilibility. Within six years of publication of the SlIqJtomycin trial. another trial dmmatically exhibited the unlRCedc:nled power of the new methodololY. The field trial of the newly de\'eloped Salk. vaccine for the pI'C'VClllion orpoliomyelilis was an enannaus effod. Centrally coonlinalc:d at the University of Michigan by a group convened for that purpose. it involved public health departments in 44 of the 48 states or the USA. Within about a 6-wc:c:k period. rrom 26 April to 15 June 1954. 402 000 childrm ft'Ceived either the SaJk ,·accine or placebo by random assignment. The very llUle numbers were n:quiMd because of the n:lalively low attack rates of the poliovirus in normal papulations of childn:n. The trial showed that the vaccine etrectively n:duccd the incidence of polio and. by provicliRi rough estimates of effectiveness for certain subgroups. sqgcstecl that the effectiveness of vaccinalion varied somewhat acconliq to the primary manifestations of the: disease (bulbospinal venus spinal) and accanlinl to the type of virus recoverai. 11K: comprehensive report describing. this heroic etrort and its n:sults (Francis ~'QI•• 1955) was publi&bcd less than 2 years after the National Foundation ror Infantile Paralysis fint annoullCed its decision to sponsor a formal trial of the vaccine. Since then. usc or the randomisc:cl prospectivc methodology has ~d. Bolstered by subsequent developments in stalistical methodology. the randomised clinical trial is
_______________________________________________________
widely acknowledged as lhe ·JOId Slandard' of evidence for evaluating lherapies. Howcver, because lhc nndomised trial can only be employcci 10 addn:ss a small fracti.. of lhc unanswen:d quellions Mlalilll to medical intervenlions. a variety of methodologies - cxperimenlal and observational. prospective and Mtraspcctive - have beea and wnlinue to be widely usc:d.. The statistical framewcn of a randomised clinical bial involves lwo sets of basic .u..s: TYF£ I BlROR ndc. P-VALIJE and validity; lOWER and precision. 'I1Ie T.""Pf! I error ral~ is the probability that if the tmatmcnts under studyclo noidilTer(i.c. the: NUU. HYPOJIIESIS islnle), the stud)' will show a statillically significant diffen:nce belwec:n them. The P-1Y1111e is the probability under the null hypolhesis ....t data would show by ch~ D diffeMnce as Imgc as lhc diR'en:nc:c obsem:d. Validit,. in clinicallrials MrClS nOl to the c:om:ctncss or the answcriDanyparlic:u1arbial but to the:eXpcclati.. that. under the: null hypoahcsis.lhc data would beIIave ina wuytxlDsistent with lhc pn>spccified Type I cnor rate and that if the sample size wen: large eaaugh.the estimated balment effect would be the lnIe effecL Power. by the same talen, is the pmbabilit)' that the study will show a stalistically silniftc:ant elTec:I or lmdmcnt if the true effect ofbatmcnt is nol zero.. PoweI'is lhen • function or the IJue effect: the larger the effect. the higher lhe power. Precision is a measwe of the variability or the estimated elTcct of_alment. The higher abc sample size and the lower the undc:rIyilll wriability or the measumncnts. Ihe higher the precisi... Results from studies of intervenlions m.y help ph)'sicians decide on the best lhcrapeulic option ror panicular patients. They pennit Mgulatory agencies to approyc products for mmetillland widespn:ad commen:ial distribution. Iac:reasingly. governments. insunmc:c companies and 1I1DII8g~ orpnisations use such studies to help decide which therapies to n:imburse. The use of fonnal clinical data as the basis for these decisions lalS on two obviausassumptions. The first is thailhe studies that f'onn the database have in fact yielded c:om:ICt n:sults: Leo an)' dilTeJaM:lCs in outcome: can with wnfidcnce be attributed 10 dilJeMDCes in Ihe therap)' adminiSlc:n:d. To lhe extent that studies passcss lhis quality, they an: said to have inielfllli validity. 1'bc: second is that the study MSUItS an:. to some dcp-ee at leasl. genemJis.ble to a population of subjects that is bmadcr than the study popuIatioa rrvm which the dDlD an: derived. Studies having this property an: said 10 hayc ~.~Iemtll .Yllitiil,. aad the broadness of a study's extemal validity is one critical meaSIR of the study's overall imponancc. A study lacking internal validil), has no n:deeming value. 'J'be men: pn:senc:e of inlc:mal validit)'. however. does DOl guaranlcc its general usefulness if the saudy has very limited extcmal validity. For example. selectilll D very lightly deftned stud)' population that docs not n:pn:scnt the: Iaqer
CUN~AL]R~~
universe of patients with the same condilion may Mndcr the lesuhs at best nanowly applicable. Alternativel)'. perhaps the interventi.. under stud), is of such technical complexity thai it is only available in D few selectc:da:ntn:s and cannot be applied bJoadl)'. Examplesorsuch problems have occ:UIIaI in virtually every fteld of medicine. 1bc major bmiClS to intemal validi!y n:1aIc mainly to the extent to which lIRe major soun:es of confusion an: pcnniltcd to interfeM with unambiguous infeJaM:IC - bias. confounding and chance (Hcnnckens ucI Buring. 1917). Usc:d in lhe wntexl or analytic clinical studies. 'bias' does not connate moral opprabrium but simply ~fen to any sy&lematic cnor in the design or execution of • saudy thai distorts lhe lnIe n:lalionship belween intervention and outCOnIC. Bias CaD originate with eilher Ihe investigators or the lIud)' subjects and is of several lypes. Sometimes the very manner or selecting a study's panicipanlS introduces bias (selection billS): this is a particular problem. ror example. in C'ASE-CmmtOL STUDIES when the selection of cascs. or ~ ment or the patient to participate. is nol indcpcadent of the chance thailhc patient will have been cxpasc:d to lhe inlervention or inteMsL In retrospeclive studies.. the ability of patients to ~I inlerYealions in the past may be inftuenced by whether or not they have expcric:accd certain medical outcomes (RECAlL BIAS). The history obtained &om a palienl in an)' lIud)' may be skewed by knowledge on the pari of eilher the interviewer (obxr1'er bia) or the study subjecl (subject bitu) ofb nallR ofdae study or what inll:rventions have occurMd or whal outcamc:s lhcy have experieaccd. In prospective studies.. lasses to follow-up oftca occur; nonrandom losses that occur dilfen:atially in one: group or lhe alhe:r may inlnxIuce serious bias. By far the best insurance agai..t the various types of bias in clinical studies is lhc use of. prospeclive. rancIomiscd lIudy design thai keeps both the inYCsIigDlolS and the study subjects unawaM of which inlervenlion the individual subjects an: n.x:civing (the so-called double-blind or double-mtUk~d desip). Certain study designs. such DS abase that compare a surgical 10 • medical intervealion or those WheM the siclc-effeclS of tn:almenl fn=quently ~veal the naturcoflhe therapy. preclude blinding of either subjects or investigators. These cases n:quire the 1IID51 objective c:adpoints avail.ble (e.g. death from any c.use:. if this is an apprupriate mc:asun: of batment effectiveness). W~ less objective endpoints an: the most meaningful meclic:ally. evalUalol'5 wIIo an: blind to the therapy received should assess them. In designs that an: nol praspcctive aDd nndomised. minimisation of biDs poses a major challellle because there arc no good analytic tools 10 cam:cl ror it. Once biDS is pn:scnt. the extenl 10 which il has been climinalcd by sound design and caaduc:1 is always open toqueslion. 1bc primary advaDtageofa wll-aJftductcd randomiscd clinical biaI is thai it n:moves many saun:cs of bias.
71
CUNICAL TRIALS _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ __ Conroundinl refers to the distortion of lhc association between intervention and outcome by the association of another factor (the mn/tRIIltle,) with both. A factor A is a confounder of an intervention I and an effi:ct E if A has an effect on E independently or J and the use of I depends in some way on A. For example. if one were to try to compare two regimens for leukaemia (sa),. a vigorous and a more gentle one) by reviewing past series of patients lreatcd with each. one miJ;ht find that the agressive regimen perfonncd much beuer than the olhcr. A more detailed analysis, howeYer. might reveal daat the agressive regimen was used pn:fcrenlially in younger palienlS, while Ihc genlle treatmenl was n:servcd for older patients. Age would mnfound any attempt to aJlDpare the two regimens in this simple manner. sinec it is well known that )'ounger leukaemia palients have a bc:lter propI05is than eldc:dy ORCS when treated with Virtually an)' relimen. Note daat. in contrast to bias, confounding is nobodY's faull. It docs not represent c:mxs of commission or omission. but rather is a natural consequence of the often complex relationships amonl the many ractors that determine clinical outcome followiRl an inlcrVention (or. II1C)m generally. following exposures of any kind). In aBSERVAnON."'- STUDIES. when a variable is suspected of being a SDU~ of confoundinl. one allemptsto corrc:c::t for the confounding in either the design or the analysis. A prospective randomiscd desiln proVides the SllOngest protection &pinst confounding because randomisation tends to equalise the distribution or potential or actual con rounders amorq; the various b'eatment anus. Randomisation does this with both known and unknown confounders. While statistical methods arc available for adjusting for known confounders. nothing other than mndomiSDlion can even approach the control or unknown conrounders. The very nature ofdinical investigation permilS the play of chance to deal the investigator a misleading answer. The reliability of a result is in pari a function of the number of patients studied: incn:asing the sample size of any nndomised study. no matter what the design. will dcc:n:asc the probabilily thai the patients studied an: peculiar in some idenliftc:d or unidentified manner. Moret:Wer. an inadequate sample size dearly incn:ascs the likelihood that chance alone can deal a false or misleadirq; resulL A trial that is too small may end up showiRl a diffen:nec where none really is prescnt or. more commonly. may fail to show a difference whcrc a medically important one really does exist. The statistical procedure thai evaluates the degmc to which the obsem::d n:sult is consi!ilc:at with chance is called a lest of statistical signf/ironce. The great vinue of randomisation is daat it removes selcc:lion bias from the allocation of palients to thenp)' and that it lends to equalise baseline paticatduuactc:ristics (actual
or potential confounders) in the various anns of the study whether these characteristics an: known or unknown. ThUs. if the sample size is sufftciently large. any slatistically significant differences in outcome can be aUribulcd to Ihc differences in therapy with much greater confidence than with other methodololics. Finally. mndomiscd In:atmc:nt assignment provides thcon:Iical support for the inference that permits calculation of Ihc probability that the obsc:ncd differences mighl have arisen by chance (the P-value). n.e conclusions or a clinical trial an: usually staled in probabilistic terms: therefCR.. even when a trial has shown a stalistically significant diffcrcna: bc:lwccn two tn:almcnts. there remains the possibility that the results might ha\'e been due to chance. If. however. several independent trials show a consistent effect. the probability that Ihc result can be ascribed to chance is enormously reduced. In such a case. chance plays a far smaller role in inlcrferinl with a sIrorq; eonclusion that it docs in most other aspcc:1S of daily life. Various features of the randomiscd controDed trial. when laken together. form the most reliable roule towards Ihc documentation of a causal n:lalion between an intervention and a clinical outcome. The prospective collection of data. wida suitable measures to ensure mrrcclneSs and completene~ serves to minimise ).IJ5SJNO DATA. misc:1assific:d data or emmcaus dDIa elements. The usc of blinding, whenevCl' feasible. minimises the presence of observer or subject bias. The use of a PUCEBO. when medically appropriate. allows isolalion or the true effects of the tesl therapy from those alIc:ndant on the Ihcrapeutic setting in general. The conlemparanc:ous relationship of lest and eonlrolgroups eliminates sc:cularchanges in patient selection or ancillary therapy that might affect results. Finally. as already described. the usc or randomisation lends to equalise the distribution of confounding variables. known and unknown. among the intervention options and proVides a formal basis for the application or statistical infen:nce 10 the data. or coune. a mndomised controlled trial is not the only route to truth. Few would quibble with the claim that appendectomy cures acute appendicitis. that penicillin cures pnc:umoc:oocaI pneumonia. that mdiothc:npy cures early HodIkin's disease or that the use of pamc:hutcs saves people who jump from planes (Smith and Pcll. 20(3). althoulh no randomised data exist to support any one of these claims. In the prcscnec of striking clinical elTms. formal lesting of a clinical hypothesis with a randomised trial may be unnecessary. Neither docs a randomised trial nc:ccssarily always give the right ansWel'. Ukc any other scientific experiment. a clinical trial is fallible. CaRless data collection, inaccurate observations, inadequate sample size. faulty tc:chniques of infen:nce or simply the play or chance can n:sull in misleading or frankly c:noncous mnclusions.
_________________________________________________________
Adherence to high standards of design. conduct and analysis. as best one can judge from abe published report. tends to bolster the cn:dibility of the trial The larger the difl'emlce in outcomes between control and test therapies. the larger the sample size (or in trials that COWlt aocnts, the more events) and the smaller the P-vaIue of the comparison and the more precisely eSlimaled the differences, the more cmlible abe n:suIts. In rancIomised controlled trials. as in other experiments. the design should address the question at hand. A clear medical question leads to a crisp design. while a fuzzy purpose may lead to an inadequate amount of data. conceotration on irrelevant details and failum to answer useful questions. In practice. many trials ha\'e founden:d because their vaguely articulated hypotheses havc spawned inadequate designs. One should think the scientiftc hypothesis underlying the clinical experiment makes scnsc, for the more biologically plausible the hypotheses the mCR likely the results will be believable. T~ is often much subjectivity hen:. however. and what makes eminent sense to some may be implausible 10 others. One may. from time to time. be raced with results in clinical trials that seem to havc no plaUsible scientific suppon. Many of the most impmtant clinical trials have been rounded on hypotheses about the pulalive mechanism of action of abe intervention. It is gratifying when such trials tum out positive. since then the result is alRsistent with the proposed mc:daanism. In the rcal world. however, it is often exllaOrdinarily difficult to usc clinical trials productively as probes for the undcdyin; mechanism. A randomiscd controlled clinical trial has a protocol that discusses the pwpasc of the trial. describes the procedures to be used and defines the endpoints as well as the criteria used to define 'success'. It justifies Ihe sample size. the study group. the strata - if aD)' - and plan for foUow~p and the methoclto be used for monitori~ safety during the course of the trial. Regulatory bodies ollen n:quire that they review protocols for trials performed for Ihe purpose of licensing a product or extending abe inclic:ation in the label. The complexity of the stud)' and ofthe pralocol depends on a number of factors. A small single-cenlR trial Ibat is slUdying a shon-ccnn intervention for symptomatic miter may have a brief protocol, while a large., multicentrc study measuring a complicated endpoint in subjects followed for sevenl yean may RXluim a much mon: detailed pnilocol. Whether the protocol is simple or CXIIIIpUcated. it should be written clearl)' and essenlial pIIIts should be easily identified. Other documents ma), provide a rurther description of the slUdy. For example, a data analysis plan may pn:sent the details of the statistical methods to be used. If the study has a data sarety monitori~ commillcc or an endpoint commit-
CUN~AL1R~LS
tee., their charters will describe them and abeir roles. The InlCrDlltional Conference on Harmonization. in ilS guidelines for Oaod Clinical Practice. describes elements of a wellconstructed protocol. While randomisation produces study groups with equal expected disbibutions of both measun:d and unmcasun:d characteristics at baseline. randomisation by itself cannol ensun: that the results of a study will be unbiased. The unbiasedness confem:d by randomisation n:quires a statistical analysis that classifies people according to the tn:aIment to which they wem mndomised. not the ~nt they actually n:ccivcd. Analysis that preserves abe randomisation is called inlenl-lo-trl!Ql aDalysis. A perfectly conductc:d clinical trial would have no problem analysing the groups as they were mndomised. for each person would n:uive the assigned therapy, each would adhen: to abe protocol and each would provide a measurement for the primary endpoinL Even rigorously CJCCCutcd clinical trials. however. ran:ly meet this ideal. Many participants in trials adhcn: incompletel)' or not at all with abeir assigned n:gimen. The prinwy endpoint may be missing for some participants. Thus, while Ihe principle of performing statistical analysis according to the randomiscd assignment is central to producing an unbiased n:suIt, in practice one is oRen forced to violate those principles. One needs reasonable approaches 10 assigning outcomes when actual observations arc unavailable. ORen investigators an: templed to analyse data from the subset of participants who complete the study according 10 the protocol. Such analyses can be subject to seven: selection biBS (Lamm el al, 1981). Sometimes an analysis oIher than the intent-to-tn:aI analysis is appropriate. For example. in studies of infectious disease whem treatment is given presumptiveI), hefon: determination of the infecting orpnism. the primary analysis may include only those patients who have an DIIIanism apilWl which the agent being studied is likel), to be effective. Such an analysis leads to an unbiased assessment of the effect of Ihe intervention on people infected with the target cqanism. A clear objective along with focused hypotheses will dri\'e the choice of endpoints. When the endpoint is unambiguous. ilS deftnition and measun:ment is simple. The mCR subjective the endpoint. the mon: need for independent 8S5Cssment. For example. in unblindcd trials of cancer aberapies when: the endpoint is a measurement of change in tumour size BS assessed by a CT SCaD. independent n:aders who do not know whether the subjects are in abe treated or control group may be n:quin:cllo ensun: unbiased measuremenl of size of Ihe tumours. lfthe endpoint is a report by the subjecl (e.g. a scon: on a scale measuring pain). abe trial may use sc\ocral outcomes to support and conuborate the prinuuy endpoinl. Control groups an: essenlial to the design of a randomised conlmlledtrial andlhc infen:nccsthat CaD be drawn fromthcm.
73
CUNICAL VERSUS STATISTICAl. SIGNIFICANCE _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ __ 1'he conllUI can be a placebo. usual CIR, a diffe~nllhempy or usual care plus a placebo. In selecting a atntlOl therapy. the invesligalOrS should choose one lhaa is ~evanllO the queslion at hand and should allempL insofar as possible. to choose: a controllhat allows blinding. The study group in a randomiscd controlled trial is necessarily helCrogencouS. Sometimes. investigators want to ensure equal allocation of lrCabnent and atnllUl in spcc:iftc subgroups. In such cases. they define slnla and randomise within strata. For example. in a sludy of p~,,.ention of heart allack, one might sInltify by OCCW11:nce of a prior heart allack. 1be choice ofwhclher or not to stratify should depend on the size of the sludy and the relationship of the particular variable to the outcome of inleR:Sl. If a variable has the potential to be a strong confounder and the study is small. then stratiticalion may be useful. At the end of a study. one might want to analyse the data by subgroup. either those IIud defined thenndomisation strata or others. The purpose of such analyses is sometimes to assess whether the treatment is efTc:ctive within specific subgroups of the population and sometimes 10 assess whether the elTc:ct of lrCatment varies by subgroup. Such analyses should be undertaken and intcrpreted with great caution because lrials arc rarcJy large enough to suppoIt reliable infen:ooe within subgroups (Yusuf el at.. 1991). While nndomised controlled trials ha\'e great advantages over other designs in tenns or producing wlidity inference about the effect or treatment, they have severe limitation in the actual selling of clinical investigation. A prospeclive trial is often large. complex and expensive, requiring the coordination or a small DImy of participants and many sites spread over counties, countries or continents. There is no realistic prospc:ct. the~ro~. of employiRJ: the nndomised clinical trial in more than a small proportion or the uruaol\'ed questions in therapy. Within spc:ciftc disease categories. the restrictive ELtOIBIUTY CRITERIA of many trials mean that the results of the study will be directly applicable only to a narrow segment of the total patient population with that disease. Sometimes. a trial would need to be very long to yield clinically meaningful results. The polio vaccine trial realised its scienlific goals quickly because the effect of the vaccine could be determined oyer the few months following immunisation. It is another matter entirely to assess the impact of a screening intervention or IRvcntive drug on the incidence of heart attacks or canc:cr; here the nc:cessary follow-up time may be measured in decades. Even for bials that determine the endpoint or individual treatments quickly. slow accrual may make the study take so long to complclC that the therapeutic question it poses is no longer or inten:st by the time the answer is available. Some subspccialties have particular problems with the use of the nndomised controlled trials; for sllllery. in particular, the acceptance
and application of the randomised trial has been slow. Finally. a randomised controlled trial may not be usable at all if the compeliRJ: interventions ha~ been in use forenoulh lime that the atliwdes of physicians are fixed: physicians are understandably reluclmllto randomise palients ir they think they already know the answer. The decision to perform a randomised controlled lrial n:quin:s a sizeable commitmenl in time. money and effOI1: the dc:cision nolto perform one entails some sacriftce in the quality of e\'idence provided 10 physicians when they arc making choices for thc:npies for their patients. A combination of medical, societal and financial forces delCnnines those questions that become the subject of randomised aJlllIUlied trials. JW AlIDa 1948: The controlled ~utic: llial. BntUlt Met/itol Jourlftll 2. 791-2. Franc" Jr, Tolf III. 1955: An cvallllllion of the 19S.
poliomyelitis vaccine trials. Summary n:pol1. Nn~rimn Journolof Pub/it Hmllir 45. 1-5 I. FriIcIInan, L M., Furbeq. C. D, lind DeMtts. D. L 1998: Fundanlerllal.s 0/ dinicallrials.3n1 alition. Heidelberg: Sprin&'Cr ~rtag. Heanebas, C. H. and Burl. J. Eo
1987: Epidemiology in medicine. BosaoD and Toronto: Linle. Browo and Co. Laaua. G"" Gl. 1981: Inftuence or tn:abncRt adhen:nce in the coronary ~ ...,ject. Nett' Engkmd Journal of Medicine 304, 612-13. ManbalI,G.,BlaeIclac:k,J. W.S.,Camena,C""aL 1948:
Streptomycin ImIbnc:nt of pullnOlllr)' tuben:ulos~ A Medical Rcsean:h CouDCil iam:stiplion. BriJisli Mediall JOUfIlQI 2. 769-82. Me_.... C. 1998: CliniEol tria/.s. NC\\' York: Oxford Unh'ClSit)' Press. Pac:ocl. S. 1996: C/inim/lriols: a procliEol approocIJ. New York: Jobo Wiley" Sous, Inc:. Sad.... G. C. and Pili, J. P.2003: Paracbute use to prcvcIIt deatb and major tnwma n:lak:d to p8\'ilaIionai cllalleqc: systematic n:vic:w ofrandomised controlled trials. Bntislr Medical JoumaI327. 1459-61. YuuI', S., Cal..... R. and Plto, R. 1984: Why do 'We need some large.. simple randomized mals? Stotistits in Medidne 3. 4O!J-20. Y......, S., "'..... J., Prabst8eId, J. aDd 1)roIer. H. 1991: AnaI)'sis and intcrprdalioa of treatmeDI c:frects in subpoups of palieDts iD rucIomimI clinical mals. Journal of lire Anreri(QII Medical Ass«iation 266. 93-8.
clinical versus statistical significance
This pair oflCnns is often confused. being mistakenly considered as interchangeable. when. in reality. neither implies the other necessarily. One oflhe UMC:Cessary c1imculties of statistics is that we arc using ordiruuy English words. such as 'normal'. "confidence' and "population', in a lCchnical way. If only our founders had followed the example of the anatomists and named everything in Lalin. It islOo late now and we arc stuck with our English lCrminology. or all the words our p~ cessors appropriated. the one that must cause the greatest confusion is "significant". 11ac Shorler OAford English DicliollOI)' gi'les Iwo definitions of "significance': "the meaniRJ: or import of somelhiRJ:. meaning. suggcsti~ness' and "imponancc, consequence'. The stalisticm lISaIe n:lales to the first interpretation. If a diffenmce is significant in a sample, there is evidence that the
_ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ CLUSTERANALYSIS IN MEDICINE difrcn:ace exisls in the population that the sample represents. Hence the difference has meaning beyond the individuals who make up the sample. By clinical significanc:e. we mean thai the different'lC we havc observed is important: that. for example, it implies that we should cluiage clinical practice. Thus. this usage ~Iates 10 the second inlelJRUtion. meaning thai the significant difference is importanl. If a diffe~nce or ~lationship is slalistically significant. this implies Ibat we havc evidence that it is real. existing in the larger population. but not that it is important. having implications for clinical IXBClice. Concluding that a difference or relationship is important depc:Ads on its magnitude. together with nonslalistical factars. so that we can decide whether it is big enough to inftlJC:llCle clinical dc:cisions. For example. in a large clinicallrial with 2000 subjecls in each ann. adiffcmlCe of I mmHg in mean diastolic blood prasurc would be statistically signiftcant. As this was a trial. il would be reasonable to conclude that the difference was ~I and thai the In:alments had slightly differenl effects on blood pressure. Yet it is unlikely that such a difference would inftucnce treatment decisions. It would not be important and so not clinically signiftcanL Conlnlriwisc, a small study might produce a nonsigniftcanl diffe~nce that is quite 1aJ];e. We could not conclude that the difference was n:al. but we might think it important enough to carry out another lrial. Statisticians cannot expeClto approprialc ordinary English words and then demand that their use be restricted. HO\\'evu. the use of "significant' in resean:h ~pol1s to mean something other than statistical sipiftcance can be potentially misleading and it makes sense to a\'Oid iL In its instructions to authors. the lmrl:el asks that authon "avoid non-tcchnical uses of Icchnicaltenns in statistics. such as .•. ..significant.. '. JMB lSec also CJlI11CAL AJIIIRAISALJ
cluster analysis In medicine The term cluster analysis coven a very wide range of methods for disc:overing groups in multivarialc data. II is distinct from classification techniques such as DlSCRo.oNANl' FUNC'IKlN ANALYSIS or cla$ijkotion tmd regre:r.sion tree (CART) (sec TREE-STRU("J1JRED ),fE'I'IIOI)5) analysis. Thescclassify individuals into groups thai have already been identified wheras cluster analysis looks for groups within the data. Oenerallcxts on cluster analysis ~ by Everilt., Landau and Leese (200 I) and GonIon (1999) and lCI::hnical developments arc often published in the Jownat of Claslqicalion. HO'MWCI'. then: is a vast lilelature dealing with cluster analysis in various guises and this is necessarily a \'el)' brief review or the m~ Widely used methods. Many specialised methods dealing with particular subject malten have become sepanlted from mainstream cluster analysis, oRcn using their own terminology. and they may be classifted under other headings such as
pattern n:cognilion. AR11FICIAL JNl'B.LIOENCE or ,"TA MOONO IN MEDICINE.
In medicine. the cases to be clustered are generally people and the multivariate data describe various aspects of their clinical. psychological or sen'ice use sIalus. However. other lD1its of analysis can of cowse be clustered. e.g. hospitals or health authorities. and cluster analysis can also be used 10 group variables. although this is less common. The data may be in the form of aUributes. such as ethnic group. or continuous measurements such as blood pressu~ or a mixture of both types may be analysed (mixed mode data). Thcobjccti\'e of the analysis is to nnd subgroups or people who arc relatively homogeneous with respect to thescclwactcristics. The reason for performing the analysis might be administntive (e.g. to define SInda in a llUl'\'Cy sample) or. IlIOn: usually. it might be ~Iatcd to a resean:h question (e.g. 10 identify groups of people with a common gene stRICture). (A review of metbods used in medicine is given by McLachlan. 1992.) In the most widely used methods. one typically pmceeds by choosing a measure of the proximity bctwccn cases in tenns of the multivariate data (the tenn "proximity' coyers both similarity and distance. either of which may be calculaIcd). Next. an algorithm for fonaing clusters is applied to the matrix of proximilies. The investigator usually has 10 decide on the number of clusten forming the ·solution'. i.e. a partition of the dala based on a particular choice of proximity measure, algorithm and number of clusters. The choice or number of clusters is particularly difficult. since the~ are few reliable formal tests and the investigator may have 10 consider a range of solutions Ihal seems reasonable based on the subjecl matter. The robustness of the final solution can be tested in a number of ways. These include using alternatiye clustering melbods. using 3pIil-_" methods on the data. the detection and exclusion of outJien or inftuential cases and validation against external data. FonnaI hypothesis tests of the NUlL HYI'OTHESIS of absence of clustu SlnIcture are theoretically possible but arc nucly applic:d. The definition of proximity between indiYiduals depends on the type of data and the relative weight 10 be placed on differenl variables (Everitt. Landau and Leese. 2(01). For example. binary attribute data may be wcled as series of ones and zeros. denoting pn:sence or absence of an atlributc. In the case w~ each category is of equal weight., such as genderor white/nonwhite ethnic group. a simple matching coeJJicienl (the proportion ofmalchcs betwec:a two indiYiduals) could be used. However. if the attributes we~ the prese~ of various symptoms. proximity might be more appropriately measun:d using the asymmetric Jaccard coefficienl. based on the proportion of matches where there is a positive match (i.e. ignoring joint negative matches). For continuous data. the Euclidean tlistllnce betweea individuals i and j.
75
CWSTER ANALYSIS IN MEDICINE _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ _ __
r~
(Xii -."Cjt) 2] 1/2.
w~ P is the aumbel' of variables.. is
~ used (applied 10 binary cIaIa it is Ihe same as the: simple matching caellicieal). Far mixed IIIGde data. Gower's ctJe/-
Jiden' can be used 10 aJIIIbinc componc:als or cliSlancc rrona either attribute or continuous data. aIlc:r flnt scaling the continuous data 10 a 0-1 raDJC. Many allCmative pmximity IIIC8SURS haw: been prapascd to deal willa specialised types of data; e.g. in lencties binary matches may be assigned ditren:at weighlS dc:peading on the: part or Ibc genetic sequc:ace fram which Ihey arise. Hicrardlical algorilhms are possibly the IIIDSt Widely used of general purpose cluSlering mc:chads and ~ included in most ST.'1ISI1CAL PACICACES. 11Ic:y use a heuristic algorithm succ:cssivcly 10 join or divide: cluSlen on the basis of their proximily (thus beilll reramilollSqglamc:raLivcordivisive methods respcclivcly). TIle methods differ in the: way in which the interc)uslel" proximilies an: calculated from the inlainciiviclual diSlanc:cs. Sin&le linIuJ,e. rar example. uses the proximity between the closesa individuals in IWO clus1e15 to bejoined. whereas CfIIIIplele linlcoge uses the most dislant. Wtutl's method is another popular agJomeraIive method that joins clUSlen on lhc: basis or an emil" sum-of-squan:s crilerion: unlike lhe: two linkAle meIhocIs lI1CIIIioned it rc:quiaa the raw cIata (rather than jusathe proximity maIrix) to be available durinl the clUslering prvcess. Divisive meIbods ~ less commonly used than Blliomenlivc methods.. except perhaps abase specifically desipc:d for allribUle data. An example of the Iauer is the IIIOIIDI/relk di...isive method. which divides the sample a«ardina;1O the value ora single altribule aI cadi stage. the: allribute beina; chasen so as to caule the most homopnc:aus paups allhal stage. PtllytMlic tlivi8iFe methods divide ac:canlinl to a number or variables considered loIe1her. 801h ag)omenlivc and poI)'Ihetic divisive: meIhods ICnc:rally pnxIuce a IRe: diapam. or dendrogram. which shows lhe: process by which cues have been joined or diviclc:d. and this can be used to SUIPSI ahe numbel' or ciuslen present (by exam