67 6THERAPY(RANDOMIZEDTRIALS)Gordon Guyatt, Sharon Straus, Maureen O. Meade, Regina Kunz, Deborah J. Cook, PJ Devereaux, and John IoannidisIN THIS CHAPTER:Clinical Scenario A Patient with Coronary Disease and a Gastrointestinal Bleed: How Can I Best Help Avoid Vascular Events and Minimize Bleeding Risk? Finding the Evidence The Users Guides Are the Results Valid? Did Intervention and Control Groups Start With the Same Prognosis? Was Prognostic Balance Maintained as the Study Progressed? Were the Groups Prognostically Balanced at the Studys Completion? What Are the Results? How Large Was the Treatment Effect? How Precise Was the Estimate of the Treatment Effect? Example 1Example 2Copyright 2008 by the American Medical Association. Click here for terms of use. P ART B: T HERAPY 68 How Can I Apply the Results to Patient Care? Were the Study Patients Similar to the Patient in My Practice? Were All Patient-Important Outcomes Considered? Are the Likely Treatment Benefits Worth the Potential Harm and Costs? Clinical Resolution F INDING THE E VIDENCE Evidence from populations with vascular disease suggests that clopidogrel is likely to besimilar, if not superior, to aspirin in its ability to prevent vascular events in patients withstableangina, 2 allowingyoutofocusonpreventionofbleeding.Youthereforeformulate the relevant question: in a patient with previous aspirin-associated ulcer, isclopidogreleffectiveinpreventingrecurrentulcerbleeding?Searching ACPJournalClub inyourmedicallibrarysOvidsystemwiththetermsclopidogrelandgas-trointestinalbleedingidentifies3articles,oneofwhichturnsouttobeyourtarget:Aspirin plus esomeprazole reduced recurrent ulcer bleeding more than clopidogrel inhigh-risk patients. 3 You print a copy of this and the original full-text article. 4 This article describes a randomized , placebo -controlled trial including 320 patientswith endoscopically confirmed ulcer bleeding, either negative test results for H pylori CLINICAL SCENARIO A Patient With Coronary Disease and a Gastrointestinal Bleed: How Can I Best Help Avoid Vascular Events and Minimize Bleeding Risk? Y ou are a general internist following a 62-year-old man with peptic ulcer diseaseand stable angina for whom you have been prescribing low-dose aspirin, a statin,an angiotensin-converting enzyme inhibitor, and as-needed nitrates. Recently, thepatient developed an upper gastrointestinal bleed. Biopsy done at endoscopy wasnegativefor Helicobacterpylori .Inhospital,thegastroenterologistlookingafteryour patient changed the aspirin to clopidogrel (and supported his action by citinga systematic review of thienopyridine derivatives, including clopidogrel, in high-risk vascular patients that found a decrease in the odds of a gastrointestinal bleedcompared with aspirin; odds ratio, 0.71; 95% condence interval [ CI ], 0.59-0.86). 1 You use ACP Journal Club to browse the medical literature and, reviewingthe patients story, you recall a recent article that may be relevant. The patientis currently stable and you ask him to return in a week for further review of hismedications.6: THERAPY (RANDOMIZED TRIALS)69orsuccessfuleradicationofHpylori,andanticipatedregularuseofantiplatelettherapy. Participants were randomly allocated to clopidogrel 75 mg daily and placeboor to aspirin 80 mg and esomeprazole (a potent proton-pump inhibitor) 20 mg twicedailyfor12months.Theprimaryoutcomewasrecurrentulcerbleeding,andsecondary outcomes included lower gastrointestinal bleeding and adverse effects.The Users GuidesTable6-1presentsourusual3-stepapproachtousinganarticlefromthemedicalliteraturetoguideyourpractice.Youwillfindthesecriteriausefulforavarietyoftherapy-relatedquestions,includingtreatingsymptomaticillnesses(eg,asthmaorarthritis), preventingdistantcomplicationsofillness(eg,cardiovasculardeathaftermyocardial infarction), and screening for silent but treatable disease (eg, colon cancerscreening).Iftheanswertoonekeyquestion(Werepatientsrandomized?)isno,someoftheother questions (Was randomization concealed? Were patients analyzed in the groups towhich they were randomized?) will lose their relevance. As you will see, nonrandomizedobservational studies yield far weaker inferences than randomized controlled trials (RCTs).Nevertheless, clinicians must use the best evidence available in managing their patients,even if the quality of that evidence is limited (see Chapter 2, The Philosophy of Evidence-Based Medicine). The criteria in Chapter 12 (Harm [Observational Studies]) will helpTABLE 6-1 Users Guides for an Article About TherapyAre the results valid? Did intervention and control groups start with the same prognosis? Were patients randomized? Was randomization concealed? Were patients in the study groups similar with respect to known prognostic factors? Was prognostic balance maintained as the study progressed? To what extent was the study blinded? Were the groups prognostically balanced at the studys completion? Was follow-up complete? Were patients analyzed in the groups to which they were randomized? Was the trial stopped early?What are the results? How large was the treatment effect? How precise was the estimate of the treatment effect?How can I apply the results to patient care? Were the study patients similar to my patient? Were all patient-important outcomes considered? Are the likely treatment benets worth the potential harm and costs?PART B: THERAPY70you assess an observational study addressing a potential treatment that has not yet beenevaluated in an RCT.ARE THE RESULTS VALID?Did Intervention and Control Groups Start With the Same Prognosis?Were Patients Randomized?Considerthequestionofwhetherhospitalcareprolongslife.Astudyfindsthat more sick people die in the hospital than in the community. We wouldeasilyrejectthenaiveconclusionthathospitalcarekillsbecauseweunder-stand that hospitalized patients are sicker than patients in the community.Althoughthelogicofprognosticbalanceisclearincomparinghospitalizedpatients with those in the community, it may be less obvious in other contexts.Until recently, clinicians and epidemiologists (and almost everyone else) believedthathormonereplacementtherapy(HRT)coulddecreasetheriskofcoronaryevents (death and myocardial infarction) in postmenopausal women. The beliefarose from the results of many studies that found women taking HRT to have adecreased risk of coronary events.5 Results of the first large randomized trial ofwomen with established coronary artery disease (CAD) provided a surprise: HRTfailed to reduce the risk of coronary events.6 Even more recently, the WomensHealth Initiative demonstrated that HRT also failed in the primary prevention ofCAD.7Other surprises generated by randomized trials include the demonstration thatantioxidant vitamins fail to reduce gastrointestinal cancer8and one such agent,vitaminE,mayactuallyincreaseall-causemortality9andthatavarietyofinitiallypromisingdrugsincreasemortalityinpatientswithheartfailure.10-15Such surprises occur periodically when investigators conduct randomized trialsto test the observations from studies in which patients and physicians determinewhichtreatmentapatientreceives(seeChapter9.2,SurprisingResultsofRandomized Trials).The reason that studies in which patient or physician preference determines whetherapatientreceivestreatmentorcontrol(observationalstudies)oftenyieldmisleadingresults is that morbidity and mortality result from many causes, of which treatment isonlyone.Treatmentstudiesattempttodeterminetheimpactofaninterventiononsuch events as stroke, myocardial infarction, and deathoccurrences that we call thetrials target outcomes. A patients age, the underlying severity of illness, the presence ofcomorbidity, and a host of other factors typically determine the frequency with which atrials target outcome occurs (prognostic factors or determinants of outcome). If prognos-ticfactorseitherthoseweknowaboutorthosewedonotknowaboutproveunbalanced between a trials treatment and control groups, the studys outcome will bebiased, either underestimating or overestimating the treatments effect. Because knownprognostic factors often influence clinicians recommendations and patients decisionsabout taking treatment, observational studies often yield biased results.6: THERAPY (RANDOMIZED TRIALS)71Observationalstudiescantheoreticallymatchpatients,eitherintheselectionofpatients for study or in the subsequent statistical analysis, for known prognostic factors(seeChapter12,Harm[ObservationalStudies],andChapter5,WhyStudyResultsMislead: Bias and Random Error). The power of randomization is that treatment andcontrol groups are more likely to be balanced with respect to both known and unknowndeterminants of outcome.WhatwasthecauseofbiasintheHRTobservationalstudies?EvidencesuggeststhatwomenwhotookHRTenjoyedahighersocioeconomicstatus.16 Their apparent benefit from HRT was probably due to factors suchasahealthierlifestyleandagreatersenseofcontroloverlife.Whatevertheexplanation, we are now confident that it was their previous prognosis, ratherthan the HRT, that led to lower rates of CAD.Althoughrandomizationisapowerfultechnique,itdoesnotalwayssucceedincreating groups with similar prognosis. Investigators may make mistakes that compro-mise randomization, or randomization may fail because of simple bad luck. The next 2sections address these issues.Was Randomization Concealed?Some years ago, a group of Australian investigators undertook a randomized trialof open vs laparoscopic appendectomy.17 The trial ran smoothly during the day.At night, however, the attending surgeons presence was required for the laparo-scopic procedure but not the open one, and limited operating room availabilitymadethelongerlaparoscopicprocedureanannoyance.Reluctanttocallinaconsultant, the residents sometimes adopted what they saw as a practical solution.When an eligible patient appeared, the residents held the semiopaque envelopescontaining the study assignment up to the light. They opened the first envelopethat dictated an open procedure. The first eligible patient in the morning wouldthenbeallocatedtothelaparoscopicappendectomygroupaccordingtothepassed-overenvelope(D.Wall,writtencommunication,June2000).Ifpatientswho presented at night were sicker than those who presented during the day, theresidents behavior would bias the results against the open procedure.When those enrolling patients are unaware and cannot control the arm to whichthe patient is allocated, we refer to randomization as concealed. In unconcealed trials,thoseresponsibleforrecruitmentmaysystematicallyenrollsickerorlesssickpatients to either treatment or control groups. This behavior will defeat the purposeofrandomizationandthestudywillyieldabiasedresult.18-20Carefulinvestigatorswillensurethatrandomizationisconcealedthroughstrategiessuchasremoterandomization,inwhichtheindividualrecruitingthepatientmakesacalltoamethods center to discover the arm of the study to which the patient is assigned.Were Patients in the Treatment and Control Groups Similar With Respect to Known Prognostic Factors?The purpose of randomization is to create groups whose prognosis, with respect tothe target outcomes, is similar. Sometimes, through bad luck, randomization willPART B: THERAPY72failtoachievethisgoal.Thesmallerthesamplesize,themorelikelythetrialwillhave prognostic imbalance.Picture a trial testing a new treatment for heart failure enrolling patients in NewYork Heart Association functional class III and class IV. Patients in class IV have amuchworseprognosisthanthoseinclassIII.Thetrialissmall,withonly8patients. One would not be surprised if all 4 class III patients were allocated to thetreatmentgroupandall4classIVpatientswereallocatedtothecontrolgroup.Such a result of the allocation process would seriously bias the study in favor of thetreatment. Were the trial to enroll 800 patients, one would be startled if random-ization placed all 400 class III patients in the treatment arm. The larger the samplesize, the more likely randomization will achieve its goal of prognostic balance.You can check how effectively randomization has balanced prognostic factors bylooking for a display of patient characteristics of the treatment and control groupsat the studys commencementthe baseline or entry prognostic features. Althoughwe will never know whether similarity exists for the unknown prognostic factors,we are reassured when the known prognostic factors are well balanced.All is not lost if the treatment groups are not similar at baseline. Statistical techniquespermit adjustment of the study result for baseline differences. Adjusted analyses may notbepreferabletounadjustedanalyses,butwhenbothanalysesgeneratethesameconclusion, readers gain confidence in the validity of the study result.Was Prognostic Balance Maintained as the Study Progressed?To What Extent Was the Study Blinded?Ifrandomizationsucceeds,treatmentandcontrolgroupsinastudybeginwithasimilarprognosis.Randomization,however,providesnoguaranteesthatthe2groupswillremainprognosticallybalanced.Blindingis,ifpossible,theoptimalstrategy for maintaining prognostic balance.Table 6-2 describes 5 groups involved in clinical trials that, ideally, will remainunawareofwhetherpatientsarereceivingtheexperimentaltherapyorcontroltherapy.Youareprobablyawarethatpatientswhotakeatreatmentthattheybelieve is effective may feel and perform better than those who do not, even if thetreatment has no biologic activity. Although the magnitude and consistency of thisTABLE 6-2 Five Groups That Should, if Possible, Be Blind to Treatment AssignmentPatients To avoid placebo effectsClinicians To prevent differential administration of therapies that affect the outcome of interest (cointervention)Data collectors To prevent bias in data collectionAdjudicators of outcome To prevent bias in decisions about whether or not a patient has had an outcome of interestData analysts To avoid bias in decisions regarding data analysis 6: THERAPY (RANDOMIZED TRIALS)73placeboeffectremainuncertain,21-24investigatorsinterestedindeterminingthebiologicimpactofapharmacologicornonpharmacologictreatmentwillensurepatients are blind to treatment allocation. Similarly, rigorous research designs willensureblindingofthosecollecting,evaluating,andanalyzingdata(Table6-2).Demonstrations of bias introduced by unblindingsuch as the results of a trial inmultiplesclerosisinwhichatreatmentbenefitjudgedbyunblindedoutcomeassessors disappeared when adjudicators of outcome were blinded25highlight theimportanceofblinding.Themorethatjudgmentisinvolvedindeterminingwhetherapatienthashadatargetoutcome(blindingislesscrucialinstudiesinwhichtheoutcomeisall-causemortality,forinstance),themoreimportantblinding becomes.Finally,differencesinpatientcareotherthantheinterventionunderstudycointerventioncan,iftheyaffectstudyoutcomes,biastheresults.Effectiveblindingeliminatesthepossibilityofeitherconsciousorunconsciousdifferentialadministrationofeffectiveinterventionstotreatmentandcontrolgroups.Wheneffectiveblindingisnotpossible,documentationofpotentialcointerventionbecomes important.Were the Groups Prognostically Balanced at the Studys Completion?Unfortunately, investigators can ensure concealed random allocation and effectiveblinding and still fail to achieve an unbiased result.Was Follow-up Complete?Ideally,attheconclusionofatrial,youwillknowthestatusofeachpatientwithrespect to the target outcome. The greater the number of patients whose outcomeis unknownpatients lost to follow-upthe more a studys validity is potentiallycompromised.Thereasonisthatpatientswhoarelostoftenhavedifferentprognosesfromthosewhoareretainedtheymaydisappearbecausetheyhaveadverseoutcomesorbecausetheyaredoingwellandsodidnotreturnforassessment.26Whendoeslosstofollow-upseriouslythreatenvalidity?Rulesofthumb(youmayrunacrossthresholdssuchas20%)aremisleading.Consider2hypothetical randomized trials, each of which enters 1000 patients into bothtreatment and control groups, of whom 30 (3%) are lost to follow-up (Table6-3). In trial A, treated patients die at half the rate of the control group (200vs 400), a relative risk reduction (RRR) of 50%. To what extent does the loss tofollow-up potentially threaten our inference that treatment reduces the deathrate by half? If we assume the worst (ie, that all treated patients lost to follow-updied),thenumberofdeathsintheexperimentalgroupwouldbe230(23%). If there were no deaths among the control patients who were lost tofollow-up, our best estimate of the effect of treatment in reducing the risk ofdeath drops from 200/400, or 50%, to (400 230)/400 or 170/400, or 43%.Thus, even assuming the worst makes little difference to the best estimate ofthe magnitude of the treatment effect. Our inference is therefore secure.PART B: THERAPY74Contrast this with trial B. Here, the reduction in the relative risk (RR) ofdeath is also 50%. In this case, however, the total number of deaths is muchlower; of the treated patients, 30 die, and the number of deaths in controlpatients is 60. In trial B, if we make the same worst-case assumption aboutthefateofthepatientslosttofollow-up,theresultswouldchangemarkedly.Ifweassumethatallpatientsinitiallyallocatedtotreatmentbutsubsequentlylosttofollow-updie,thenumberofdeathsamongtreated patients rises from 30 to 60, which is exactly equal to the number ofcontrolgroupdeaths.Letusassumethatthisassumptionisaccurate.Because we would have 60 deaths in both treatment and control groups, theeffectoftreatmentdropsto0.Becauseofthisdramaticchangeinthetreatment effect (50% RRR if we ignore those lost to follow-up; 0% RRR ifweassumeallpatientsinthetreatmentgroupwhowerelosttofollow-updied), the 3% loss to follow-up in trial B threatens our inference about themagnitude of the RRR.Of course, this worst-case scenario is unlikely. When a worst-case scenario,were it true, substantially alters the results, you must judge the plausibility ofa markedly different outcome event rate in the treatment and control grouppatients lost to follow-up.Inconclusion,losstofollow-uppotentiallythreatensastudysvalidity.Ifassuming a worst-case scenario does not change the inferences arising from studyresults,thenlosstofollow-upisnotaproblem.Ifsuchanassumptionwouldsignificantlyaltertheresults,theextenttowhichvalidityiscompromiseddependsonhowlikelyitisthattreatmentpatientslosttofollow-updidbadlywhilecontrolpatientslosttofollow-updidwell.Thatdecisionisamatterofjudgment.TABLE 6-3When Does Loss to Follow-up Seriously Threaten Validity?Trial A Trial BTreatment Control Treatment ControlNumber of patients randomized 1000 1000 1000 1000Number (%) lost to follow-up 30 (3) 30 (3) 30 (3) 30 (3)Number (%) of deaths 200 (20) 400 (40) 30 (3) 60 (6)RRR not counting patients lost to follow-up0.2/0.4 = 0.50 0.03/0.06 = 0.50RRRworst-case scenarioa0.17/0.4 = 0.43 0.00/0.06 = 0Abbreviation: RRR, relative risk reduction.aThe worst-case scenario assumes that all patients allocated to the treatment group and lost to follow-up died and all patients allocated to the control group and lost to follow-up survived. 6: THERAPY (RANDOMIZED TRIALS)75Was the Trial Stopped Early?Although it is becoming increasingly popular, stopping trials early when one seesanapparentlargebenefitisrisky.27Trialsterminatedearlywillcompromiserandomizationiftheystopatarandomhighwhenprognosticfactorstempo-rarily favor the intervention group. Particularly when sample size and the numberofeventsaresmall,trialsstoppedearlyruntheriskofgreatlyoverestimatingthetreatment effect (see Chapter 9.3, Randomized Trials Stopped Early for Benefit).Were Patients Analyzed in the Groups to Which They Were Randomized?Investigatorscanalsounderminerandomizationiftheyomitfromtheanalysispatientswhodonotreceivetheirassignedtreatmentor,worseyet,counteventsthatoccurinnonadherentpatientswhowereassignedtotreatmentagainstthecontrolgroup.Suchanalyseswillbiastheresultsifthereasonsfornonadherencearerelatedtoprognosis.Inanumberofrandomizedtrials,patientswhodidnotadhere to their assigned drug regimens have fared worse than those who took theirmedicationasinstructed,evenaftertakingintoaccountallknownprognosticfactorsandevenwhentheirmedicationswereplacebos.28-33Whenadherentpatients are destined to have a better outcome, omitting those who do not receiveassigned treatment undermines the unbiased comparison provided by randomiza-tion. Investigators prevent this bias when they follow the intention-to-treat princi-pleandanalyzeallpatientsinthegrouptowhichtheywererandomized(seeChapter 9.4, The Principle of Intention to Treat).USING THE GUIDEReturning to our opening clinical scenario, did the experimental andcontrolgroups begin the study with a similarprognosis? The study wasrandomizedandallocationwasconcealed;320patientsparticipatedand99%werefollowed up. The investigators followed the intention-to-treat principle, includ-ing all patients in the arm to which they were randomized, and stopped whenthey reached the planned sample size. There were more patients who smoked(13% vs 8.2%) and regularly consumed alcohol (8.1% vs 5%) in the clopidogrelgroupcomparedwiththeaspirin-esomeprazolegroup.Thiscouldbiastheresultsinfavoroftheaspirin-esomeprazole,andtheinvestigatorsdonotprovide anadjusted analysis for the baseline differences. Clinicians, patients,datacollectors,outcomesassessors,anddataanalystswereallblindtoallocation.The final assessment of validity is never a yes-or-no decision. Rather, thinkofvalidityasacontinuumrangingfromstrongstudiesthatareverylikelytoyield an accurate estimate of the treatment effect to weak studies that are verylikely to yield a biased estimate of effect. Inevitably, the judgment as to wherea study lies in this continuum involves some subjectivity. In this case, despiteuncertainty about baseline differences between the groups, we conclude thatthe methods were strong.PART B: THERAPY76WHAT ARE THE RESULTS?How Large Was the Treatment Effect?Mostfrequently,RCTscarefullymonitorhowoftenpatientsexperiencesomeadverseeventoroutcome.Examplesofthesedichotomousoutcomes(yes-or-nooutcomes,onesthateitherhappenordonothappen)includecancerrecurrence,myocardial infarction, and death. Patients either have an event or they do not, andthearticlereportstheproportionofpatientswhodevelopsuchevents.Consider,for example, a study in which 20% of a control group died, but only 15% of thosereceiving a new treatment died (Table 6-4). How might one express these results?Onepossibilitywouldbetheabsolutedifference(knownastheabsoluteriskreduction [ARR], or risk difference), between the proportion who died in the controlgroup (baseline risk or control event rate [CER]) and the proportion who died in thetreatmentgroup(experimentaleventrate[EER]),orCEREER=0.200.15=0.05. Another way to express the impact of treatment is as an RR: the risk of eventsamong patients receiving the new treatment relative to that risk among patients inthe control group, or EER/CER = 0.15/0.20 = 0.75.Themostcommonlyreportedmeasureofdichotomoustreatmenteffectsisthecomplement of the RR, the RRR. It is expressed as a percentage: 1 (EER/CER) 100%= (1 0.75) 100% = 25%. An RRR of 25% means that the new treatment reduced therisk of death by 25% relative to that occurring among control patients; the greater theRRR, the more effective the therapy. Investigators may compute the RR over a period oftime, as in a survival analysis, and call it a hazard ratio (see Chapter 7, Does TreatmentLower Risk? Understanding the Results). When people do not specify whether they aretalking about RRR or ARRfor instance, Drug X was 30% effective in reducing theriskofdeath,orTheefficacyofthevaccinewas92%theyarealmostinvariablytalkingaboutRRR(seeChapter7,DoesTreatmentLowerRisk?UnderstandingtheResults, for more detail about how the RRR results in a subjective impression of a largertreatment effect than do other ways of expressing treatment effects).TABLE 6-4 Results From a Hypothetical Randomized TrialExposureOutcomeDeath Survival TotalTreatment 15 85 100Control 20 80 100Control event rate (CER): 20/100 = 20%.Experimental event rate (EER): 15/100 = 15%.Absolute risk reduction or risk difference: CER EER, 20% 15% = 5%.Relative risk: EER/CER = (15/100)/(20/100) 100% = 75%.Relative risk reduction: 1 (EER/CER) 100% = 1 75% = 25%.6: THERAPY (RANDOMIZED TRIALS)77How Precise Was the Estimate of the Treatment Effect?Wecanneverbesureofthetrueriskreduction;thebestestimateofthetruetreatmenteffectiswhatweobserveinawell-designedrandomizedtrial.Thisestimateiscalledapointestimatetoremindusthat,althoughthetruevalueliessomewhere in its neighborhood, it is unlikely to be precisely correct. Investigatorsoften tell us the neighborhood within which the true effect likely lies by calculatingCIs, a range of values within which one can be confident the true effect lies.34We usually use the 95% CI (see Chapter 8, Confidence Intervals). You can considerthe 95% CI as defining the range thatassuming the study was well conducted and hasminimal biasincludes the true RRR 95% of the time. The true RRR will generally liebeyond these extremes only 5% of the time, a property of the CI that relates closely tothe conventional level of statistical significance of P < .05 (see Chapter 10.1, HypothesisTesting). We illustrate the use of CIs in the following examples.Example 1Ifatrialrandomized100patientseachtotreatmentandcontrolgroups,andthere were 20 deaths in the control group and 15 deaths in the treatment group,the authors would calculate a point estimate for the RRR of 25% (CER = 20/100or 0.20, EER = 15/100 or 0.15, and 1 EER/CER = (1 0.75) 100 = 25%). Youmight guess, however, that the true RRR might be much smaller or much greaterthan 25%, based on a difference of only 5 deaths. In fact, you might surmise thatthe treatment might provide no benefit (an RRR of 0%) or might even do harmFIGURE 6-1Confidence Intervals in Trials of Various Sample SizeAbbreviations: CI, condence interval; RRR, relative risk reduction.Twostudieswiththesamepointestimate,a25%RRR,butdifferentsamplesizesandcorrespondinglydifferentCIs.Thex-axisrepresents the different possible RRR, and the y-axis represents the likelihood of the true RRR having that particular value. The solidline represents the CI around the first example, in which there were 100 patients per group, and the number of events in active andcontrolwas15and20,respectively.ThebrokenlinerepresentstheCIaroundthesecondexampleinwhichtherewere1000patients per group, and the number of events in active and control was 150 and 200, respectively. RRR, % 50 2502550 9 38Study A: 100 patients/group Study B: 1000 patients/group 41 59PART B: THERAPY78(a negative RRR). And you would be right; in fact, these results are consistentwith both an RRR of 38% (that is, patients given the new treatment mightbe 38% more likely to die than control patients) and an RRR of nearly 59%(that is, patients subsequently receiving the new treatment might have a riskof dying almost 60% less than those who are not treated). In other words, the95% CI on this RRR is 38% to 59%, and the trial really has not helped usdecide whether or not to offer the new treatment.Example 2 What if the trial enrolled 1000 patients per group rather than 100 patients pergroup, and the same event rates were observed as before, so that there were200 deaths in the control group (CER = 200/1000 = 0.20) and 150 deaths inthe treatment group (EER = 150/1000 = 0.15)? Again, the point estimate ofthe RRR is 25% (1 EER/CER = 1 (0.15/0.20) 100 = 25%).Inthislargertrial,youmightthinkthatourconfidencethatthetruereduction in risk is close to 25% is much greater, and, again, you would beright. The 95% CI on the RRR for this set of results is all on the positive sideof zero and runs from 9% to 41%.What these examples show is that the larger the sample size of a trial, thelarger the number of outcome events and the greater our confidence that thetrue RRR (or any other measure of effect) is close to what we have observed.In the second example, the lowest plausible value for the RRR was 9% and thehighestvaluewas41%.Thepointestimateinthiscase,25%istheonevalue most likely to represent the true RRR. As one considers values fartherand farther from the point estimate, they become less and less consistent withthe observed RRR. By the time one crosses the upper or lower boundaries ofthe 95% CI, the values are very unlikely to represent the true RRR, given thepointestimate(thatis,theobservedRRR).Allthis,ofcourse,assumesthestudy has satisfied the validity criteria we discussed earlier.Figure 6-1 represents the CIs around the point estimate of an RRR of 25%inthese2examples,withariskreductionof0representingnotreatmenteffect. In both scenarios, the point estimate of the RRR is 25%, but the CI isfar narrower in the second scenario.Not all randomized trials have dichotomous outcomes, nor should they. Inastudyofrespiratorymuscletrainingforpatientswithchronicairflowlimitation, one primary outcome measured how far patients could walk in 6minutesinanenclosedcorridor.35This6-minutewalkimprovedfromanaverageof406to416m(up10m)intheexperimentalgroupreceivingrespiratory muscle training and from 409 to 429 m (up 20 m) in the controlgroup.Thepointestimateforimprovementinthe6-minutewalkduetorespiratorymuscletrainingthereforewasnegative,at10m(ora10-mdifference in favor of the control group).Here, too, you should look for the 95% CIs around this difference in changesin exercise capacity and consider their implications. The investigators tell us that6: THERAPY (RANDOMIZED TRIALS)79the lower boundary of the 95% CI was 26 (that is, the results are consistent witha difference of 26 m in favor of the control treatment) and the upper boundarywas+5m.Eveninthebestofcircumstances,patientsareunlikelytoperceiveadding5mtothe400recordedatthestartofthetrialasimportant,andthisresult effectively excludes an important benefit of respiratory muscle training asapplied in this study.It will not surprise you that the larger the sample size, the narrower the CI. If youwant to learn more about CIs, including finding out when the sample size is sufficientlylarge, see Chapter 8, Confidence Intervals.Having determined the magnitude and precision of the treatment effect, clinicianscan turn to the final question of how to apply the articles results to their patients.HOW CAN I APPLY THE RESULTS TO PATIENT CARE?Were the Study Patients Similar to the Patient in My Practice?Often, the patient before you has different attributes or characteristics from thoseenrolled in the trial. He or she may be older or younger, sicker or less sick, or mayhave comorbid disease that would have excluded him or her from participation intheresearchstudy.Ifthepatientqualifiedforenrollmentinthestudy,youcanapply the results with considerable confidence.What if that individual does not meet a studys eligibility criteria? The study resultprobably applies even if, for example, he or she was 2 years too old for the study, hadmore severe disease, had previously been treated with a competing therapy, or had acomorbidcondition.Abetterapproachthanrigidlyapplyingthestudysinclusionandexclusioncriteriaistoaskwhetherthereissomecompellingreasonwhytheresults do not apply to the patient. You usually will not find a compelling reason, andmostoftenyoucangeneralizetheresultstoyourpatientwithconfidence(seeChapter 11.1, Applying Results to Individual Patients).USING THE GUIDEUsingtherawnumbersprovidedinthearticle,1of159people(0.6%)intheaspirin-esomeprazolegroupand13ofthe161people(8%)intheclopidogrel group experienced a recurrence of ulcer. TheRRR is 92%, andthe 95% CI extends from 41% to 99%. The very large effect and the smallnumber of events somewhat reduce your confidence in this result; 4.4% ofthe aspirin-esomeprazole group and 9.4% of the clopidogrel group had anadverseeffect(definedasdyspepsiaoranallergy).Theinvestigatorsalsoreported that 11 patients in the aspirin-esomeprazole group and 9 patientsin the clopidogrel group experienced recurrent ischemic eventsPART B: THERAPY80A related issue has to do with the extent to which we can generalize findings from astudy using a particular drug to another closely (or not so closely) related agent. Theissue of drug class effects and how conservative one should be in assuming class effectsremains controversial (see Chapter 22.5, Drug Class Effects). Generalizing findings ofsurgical treatment may be even riskier. Randomized trials of carotid endarterectomy,for instance, demonstrate much lower perioperative rates of stroke and death than onemight expect in ones own community.36A final issue arises when a patient fits the features of a subgroup of patients in thetrial report. We encourage you to be skeptical of subgroup analyses37 (see Chapter 20.4,When to Believe a Subgroup Analysis). The treatment is likely to benefit the subgroupmore or less than the other patients only if the difference in the effects of treatment inthe subgroups is large and very unlikely to occur by chance. Even when these conditionsapply,theresultsmaybemisleadingifinvestigatorsdidnotspecifytheirhypothesesbefore the study began, if they had a very large number of hypotheses, or if other studiesfail to replicate the finding.Were All Patient-Important Outcomes Considered?Treatments are indicated when they provide important benefits. Demonstrating that abronchodilator produces small increments in forced expired volume in patients withchronic airflow limitation, that a vasodilator improves cardiac output in heart failurepatients,orthatalipid-loweringagentimproveslipidprofilesdoesnotprovideasufficient reason for administering these drugs (see Chapter 11.4, Surrogate Outcomes).Here, investigators have chosen substitute or surrogate outcomes rather than those thatpatientswouldconsiderimportant.Whatcliniciansandpatientsrequireisevidencethat the treatments improve outcomes that are important to patients (patient-importantoutcomes), such as reducing shortness of breath during the activities required for dailyliving,avoidinghospitalizationforheartfailure,ordecreasingtheriskofmyocardialinfarction.38Trialsoftheimpactofantiarrhythmicdrugsaftermyocardialinfarctionillustrate the danger of using substitute outcomes or endpoints. Because such drugshaddemonstratedareductioninabnormalventriculardepolarizations(thesubstituteendpoints),itmadesensethattheyshouldreducetheoccurrenceoflife-threateningarrhythmias.Agroupofinvestigatorsperformedrandomizedtrialson3agents(encainide,flecainide,andmoricizine)thatwerepreviouslyshowntobeeffectiveinsuppressingthesubstituteendpointofabnormalventriculardepolarizations.Theinvestigatorshadtostopthetrialswhentheydiscoveredthatmortalitywassubstantiallyhigherinpatientsreceivingantiar-rhythmic treatment than in those receiving placebo.39,40 Clinicians relying on thesubstitute endpoint of arrhythmia suppression would have continued to admin-ister the 3 drugs, to the considerable detriment of their patients.Even when investigators report favorable effects of treatment on one patient-impor-tantoutcome,youmustconsiderwhethertheremaybedeleteriouseffectsonotheroutcomes. For instance, cancer chemotherapy may lengthen life but decrease its quality(seeChapter10.5,MeasuringPatientsExperience).Randomizedtrialsoftenfailtoadequately document the toxicity or adverse effects of the experimental intervention.416: THERAPY (RANDOMIZED TRIALS)81Composite endpoints represent a final dangerous trend in presenting outcomes.Likesurrogateoutcomes,compositeendpointsareattractiveforreducingsamplesize and decreasing length of follow-up. Unfortunately, they can mislead. We mayfind that a trial that reduced a composite outcome of death, renal failure requiringdialysis,anddoublingofserumcreatininelevelactuallydemonstratedatrendtoward increased mortality with the experimental therapy and showed convincingeffects only on doubling of serum creatinine level42 (see Chapter 10.4, CompositeEndpoints).Another long-neglected outcome is the resource implications of alternative manage-ment strategies. Health care systems face increasing resource constraints that mandatecareful attention to economic analysis (see Chapter 22.1, Economic Analysis).Are the Likely Treatment Benefits Worth the Potential Harm and Costs?If you can apply the studys results to a patient, and its outcomes are important, the nextquestionconcernswhethertheprobabletreatmentbenefitsareworththeeffortthatyou and the patient must put into the enterprise. A 25% reduction in the RR of deathmay sound quite impressive, but its impact on your patient and practice may neverthe-less be minimal. This notion is illustrated by using a concept called number needed totreat (NNT),thenumberofpatientswhomustreceiveaninterventionoftherapyduring a specific period to prevent 1 adverse outcome or produce 1 positive outcome.43The impact of a treatment is related not only to its RRR but also to the risk oftheadverseoutcomeitisdesignedtoprevent.Onelargetrialinmyocardialinfarctionsuggeststhattissueplasminogenactivator(tPA)administrationreduces the RR of death by approximately 12% in comparison to streptokinase.44Table6-5considers2patientspresentingwithacutemyocardialinfarctionassociated with elevation of ST segments on their electrocardiograms.Inthefirstcase,a40-year-oldmanpresentswithelectrocardiographicfindings suggesting an inferior myocardial infarction. You find no signsTABLE 6-5 Considerations in the Decision to Treat 2 Patients With Myocardial Infarction With Tissue Plasminogen Activator or StreptokinaseRisk of Death 1 Year After MI With Streptokinase (CER)Risk With tPA (EER) (ARR = CER EER)Number Needed to Treat (100/ARR When ARR Is Expressed as a Percentage)40-Year-old man with small MI2% 1.86% (0.24% or 0.0024)41770-Year-old man with large MI and heart failure40% 35.2% (4.8% or 0.048)21Abbreviations: ARR, absolute risk reduction; CER, control event rate; EER, experimental event rate; tPA, tissue plasminogen acti-vator; MI, myocardial infarction.PART B: THERAPY82of heart failure, and the patient is in normal sinus rhythm, with a rate of 90/min.This individuals risk of death in the first year after infarction may be as low as2%.Incomparisontostreptokinase,tPAwouldreducethisriskby12%to1.86%, an ARR of 0.24% (0.0024). The inverse of this ARR (that is, 100 dividedby the ARR expressed as a percentage) is equal to the number of such patients wewould have to treat to prevent 1 event (in this case, to prevent 1 death after a mildheart attack in a low-risk patient), the NNT. In this case, we would have to treatapproximately 417 such patients to save a single life (100/0.24 = 417). Given thesmallincreasedriskofintracerebralhemorrhageassociatedwithtPA,anditsadditional cost, many clinicians might prefer streptokinase in this patient.Inthesecondcase,a70-year-oldmanpresentswithelectrocardiographicsignsofanteriormyocardialinfarctionwithpulmonaryedema.Hisriskofdyinginthesubsequentyearisapproximately40%.A12%RRRofdeathinsuch a high-risk patient generates an ARR of 4.8% (0.048), and we would haveto treat only 21 such individuals to avert a premature death (100/4.8 = 20.8).Many clinicians would consider tPA the preferable agent for this man.A key element of the decision to start therapy, therefore, is to consider thepatients risk of the adverse event if left untreated.For any given RRR, the higher the probability that a patient will experience anadverseoutcomeifwedonottreat,themorelikelythepatientwillbenefitfromtreatmentandthefewersuchpatientsweneedtotreattoprevent1adverseoutcome (see Chapter 7, Does Treatment Lower Risk? Understanding the Results).KnowingtheNNThelpscliniciansintheprocessofweighingthebenefitsanddownsidesassociatedwiththemanagementoptions(seeChapter11.1,ApplyingResults to Individual Patients). Chapter 11.2 (Example Numbers Needed to Treat)presents NNTs associated with clearly defined risk groups in a number of commontherapeutic situations.Tradeoffofbenefitandriskalsorequiresanaccurateassessmentoftreatmentadverse effects. Randomized trials, with relatively small sample sizes, are unsuitablefordetectingrarebutcatastrophicadverseeffectsoftherapy.Cliniciansmustoftenlook to other sources of informationoften characterized by weaker methodologytoobtainanestimateoftheadverseeffectsoftherapy(seeChapter12,Harm[Observational Studies]).Thepreferencesorvaluesthatdeterminethecorrectchoicewhenweighingbenefitandriskarethoseoftheindividualpatient.Greatuncertaintyabouthowbest to communicate information to patients and how to incorporate their valuesintoclinicaldecisionmakingremains.Vigorousinvestigationofthisfrontierofevidence-basedmedicineis,however,underway(seeChapter22.2,DecisionMaking and the Patient).Cliniciansmayfindittemptingtoturntothearticlesauthorsforguidanceabout tradeoffs between benefits and risks. Because of the possibility of conflict ofinterest, this can be dangerous. 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