Ebm Harm Usila Saa

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AmericanMedicalAssociation

81

1B2HARM

Mitchell Levine, David Haslam, Stephen Walter,

Rob ert Cum ming , Hui Lee , Ted Haines , Anne Holbroo k,

Virg inia Moyer, a nd G ordo n G uya tt

The following EBM Working Group members also made substantive

contributions to this section: Peter Pronovost and Sharon Straus

IN THIS SECTION

Finding the Evidence

Are the Res ults Va lid?

D id the Investigators Demonstrate Similarity in All Known D eterminants of

O utcome? Did They Adjust for D ifferences in the Analysis?

Were Exposed Patients Equally Likely to Be Identified in the Two G roups?

Were the O utcomes M easured in the Same Way in the Groups Being Com pared?

Was Follow-up Sufficiently Complete?

Wha t Are the Results?

How Strong Is the Association Between Exposure and O utcome?

How Precise Is the Estimate of the Risk?

How Can I Apply the Results to Patient Care?

Were the Study Patients Similar to the Patient in M y Practice?

Was the Duration of Follow-up Adequate?

What Was the M agnitude of the Risk?

Should I A ttempt to Stop the Exposure?

Clinical Resolution


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FI NDING THEEVIDENCE

You formulate the following focused question:

Do ad ults s uffering from depression a nd taking S S RI med ications,com pared to patients no t taking antidepressa nts, suffer an increas ed

risk of se rious upper g as trointestina l bleed ing ?

Later that day, you begin your search using prefiltered evidence-based medicineresourcesthe journalEvidence Based Mental Health, Best Evidence4,ClinicalEvidence, and the Cochrane Library. For each database, you enter the term sero-tonin reuptake inhibitor. Search ofEvidence Based Mental Health yields eightreviews in volumes 1 (1998) and 2 (1999). Four of these deal with adverse effectsassociated with SSRI use, but none addresses gastrointestinal bleeding. Searching

Best Evidence4 yields 17 equally unhelpful articles.A Clinical Evidence search iden-tifies only a review on treatment of depressive disorders in adults. The CochraneLibrary search locates four complete reviews and two abstracts of systematicreviews, but none addresses the issue of gastrointestinal bleeding in SSRI users.

You now turn to the PubMed version of MEDLINE and PreMEDLINEsearching system (www.ncbi.nlm.nih.gov/entrez/query.fcgi). For optimum searchefficiency, you click on Clinical queries under PubMed Services to access sys-tematically tested search strategies, or you go to Search hedges, which will helpyou identify methodologically sound studies pertaining to your question on

harm (see Part 1A1,Finding the Evidence).You enter the following:selectiveserotonin reuptake inhibitor AND bleeding for the subject search term; andyou click on Etiology for study category and Specificity for emphasis.YourMEDLINE search (from 1966 through 2000) identifies one citation, an epidemio-logic study assessing the association between SSRIs and upper gastrointestinalbleeding.7 This study describes a threefold increased risk of upper gastrointestinalbleeding associated with the use of SSRIs. Thinking that this article may answeryour question, you download the full text free of charge from theBri ti sh MedicalJournal(BMJ) Web site (www.bmj.com) as a portable document format (PDF)fi le, an electronic version of a printed page or pages.

ARE THERESULTSVALID?

Clinicians often encounter patients who are facing potentially harmful exposures,either to medical interventions or environmental agents, and important questionsarise. Are pregnant women at increased risk of miscarriage if they work in frontof video display terminals? Do vasectomies increase the risk of prostate cancer?Do hypertension management programs at work lead to increased absenteeism?When examining these questions, physicians must evaluate the validity of thedata, the strength of the association between the assumed cause and the adverseoutcome, and the relevance to patients in their practice.

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As when answering any clinical question, our first goal should be to identifya systematic review of the topic that can provide an objective summary of all theavailable evidence (see Part 1E,Summarizing the Evidence). However, interpret-ing a systematic review requires an understanding of the rules of evidence for

observational (nonrandomized) studies. The tests for judging the validity ofobservational study results, like the validity tests for randomized controlled trials,help you decide whether experimental and control groups began the study witha similar prognosis and whether similarity with respect to prognostic factorspersisted after the study was started (see Table 1B-5).

TABLE 1B5

Users Guides for an Art icle About Harm

Are the results valid?

Did experimental and c ontrol groups beg in the study w ith a s imilar progno sis?

Did the investiga tors dem ons trate s imilarity in all know n determinants o f outcom e;

did they ad just for differences in the a nalysis?

Were exposed patients equally likely to be identified in the two groups?

Did e xperimenta l and c ontrol groups retain a similar prog nos is a fter the study started?

Were the outcomes mea sured in the sam e w ay in the groups being co mpa red?

Wa s fo llow -up s ufficiently c om plete?

What are the results? How s trong is the associat ion betw een exposure and outcome?

How precise is the estimate of the risk?

How can I apply the results to patient care?

Were the study patients similar to the patient under consideration in my practice?

Was the duration o f follow -up ad eq uate?

What w as the ma gnitude o f the risk?

S hould I attem pt to stop the expos ure?

Did the Investigators Demonstrate Similarit y in All Know n Determinantsof Outcome? Did They Adjust f or Dif ferences in the Analysis?

Studies of potentially harmful exposures will yield biased results if the groupexposed to the putative harmful agent and the unexposed group begin with a dif-ferent prognosis. Let us say we are interested in the impact of hospitalization onmortality rate. To investigate this question, we compare mortality in hospitalizedindividuals to that in people of similar age and sex in the community. Although anexamination of the results would lead us to stay clear of hospitals, few would takethese results seriously. The reason for skepticism is that people are admitted tohospitals because they are sick and, therefore, are at greater risk of dying.Thishigher risk results in a spurious (that is, noncausal) association between exposure

USERSGUIDES TO THEMEDICALL ITERATURE84

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(hospitalization) and outcome (death). In general, people who seek health careor who take medicine are sicker than people who do not. If clinicians fail to takethis into account, they are at high risk of making inaccurate inferences aboutcausal relations between medications and adverse effects.

How can investigators ensure that their comparison groups start a study with asimilar likelihood of suffering the target outcome? Randomized controlled trialsprovide less biased estimates of potentially harmful effects than other studydesigns because randomization is the best way to ensure that groups are balancedwith respect to both known and unknown determinants of outcome (see Part 1B1,Therapy). Although investigators conduct RCTs to determine whether therapeu-tic agents are beneficial, RCTs can also demonstrate harm. The unexpected resultsof some randomized trials (for example, drugs that investigators expected to showbenefit sometimes are associated with increased mortality) have demonstrated

the potential of this study design for demonstrating harm (seePart 2B1,Therapyand Validity, Surprising Results of Randomized Trials).

There are two reasons that we cannot usually find RCTs to help us determineif a putative harmful agent truly has deleterious effects. First, we consider itunethical to randomize patients to exposures that may be harmful (not beneficial).Even if we did not hold these scruples, informed patients would not consent tosuch an experiment.

Second, we are often concerned about rare and serious adverse effects thatoccur over prolonged periods of timeones that become evident only after tens

of thousands of patients have consumed the medication. For instance, even a verylarge randomized trial8 failed to detect an association between clopidogrel andthrombotic thrombocytopenic purpura, which was detected by a subsequentobservational study.9 Randomized trials specifically addressing side effects maybe feasible for adverse event rates as low as 1%10, 11 and meta-analyses may be veryhelpful when event rates are low.12 The randomized trials we would need toexplore harmful events that occur in less than one in 100 exposed patientstrialscharacterized by huge sample size and lengthy follow-upare logistically difficultand prohibitively expensive.

Given that clinicians will not find RCTs to answer most questions about harm,they must understand alternative strategies for ensuring a balanced prognosisin the groups being compared. This understanding requires a familiarity withobservational study designs, which we will now describe (Table 1B-6).


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TABLE 1B-6

Directions of Inquiry and Key Methodologic Strengths and Weaknesses forDifferent Study Designs

Design Start ing Point Assessment Strengths Weaknesses

Cohort Expos ure status Outcome event Fea sible w hen S usceptible to

status rando mization b ias , limited

of exposure va lidity

not pos sible

Cas e-Control Outcome event Expos ure status Overcome s S usceptible to

status tempo ral delays , bias, limited

m a y o nly va lid ity

require sm all

sa mple size

RCT Exposure sta tus Adve rse even t Low sus ceptibility Fea sibility,

sta tus to bias g enera liza bility

Cohort StudiesIn acohort study, the investigator identifies exposed and nonexposed groups ofpatients, each a cohort, and then follows them forward in time, monitoring the

occurrence of the predicted outcome. In one such study, for example, investigatorsassessed perinatal outcomes among infants of men exposed to lead and organicsolvents in the printing industry by means of a cohort of all males who had beenmembers of printers unions in Oslo.13 The investigators used job classification tocategorize fathers as being either exposed to lead and solvents or not exposed tothose substances. In this study, exposure was associated with an eightfold increasein preterm births, but it was not linked with birth defects.

Investigators may rely on cohort designs when harmful outcomes occur infre-quently. For example, clinically apparent upper gastrointestinal hemorrhage inpatients using NSAIDs occurs approximately 1.5 times per 1000 person-yearsof exposure, in comparison with 1.0 per 1000 person-years in those not takingNSAIDs.14 Because the event rate in unexposed patients is so low (0.1%), a ran-domized trial to study an increase in r isk of 50% would require huge numbers ofpatients (sample size calculations suggest about 75,000 patients per group) foradequate power to test the hypothesis that NSAIDs cause the additional bleeding.15

Such a randomized trial would not be feasible, but a cohort study, in which theinformation comes from a large administrative database, would be possible.

The danger in using observational studies to assess a possible harmful exposureis that exposed and unexposed patients may begin with a different risk of thetarget outcome. For instance, in the association between NSAIDs and theincreased risk of upper gastrointestinal bleeding,age may be associated both withexposure to NSAIDs and with gastrointestinal bleeding. In other words, sincepatients taking NSAIDs will be older and older patients are more likely to bleed,


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this confounding variablemakes attribution of an increased risk of bleeding toNSAID exposure problematic.

There is no reason patients who self-select (or who are selected by their physi-cian) for exposure to a potentially harmful agent should be similar, with respect

to other important determinants of outcome, to the nonexposed patients. Indeed,there are many reasons to expect they will not be similar. Physicians are reluctantto prescribe medications they perceive will put their patients at risk and will selec-tively prescribe low-risk medications. In one study, for instance, 24.1% of patientswho were given a then-new NSAID, ketoprofen, had received peptic ulcer therapyduring the previous 2 years in comparison to 15.7% of the control population.16

The likely reason is that the ketoprofen manufacturer succeeded in persuadingclinicians that ketoprofen was less likely to cause gastrointestinal bleeding thanother agents. A subsequent comparison of ketoprofen to other agents would be

subject to the risk of finding a spurious increase in bleeding with the new agentbecause higher-risk patients would have been receiving the drug.

The prescription of benzodiazepines to elderly patients provides another exampleof the way that selective physician prescribing practices can lead to a different distri-bution of risk in patients receiving particular medications. This is referred to as thechanneling effect.17,18 Ray and colleagues19 found an association between long-actingbenzodiazepines and risk of falls (relative risk [RR], 2.0; 95% CI, 1.6-2.5) in datafrom 1977 to 1979,but not in data from 1984 to 1985 (RR, 1.3; 95% CI, 0.9-1.8).The most plausible explanation for the change is that patients at high risk for falls

(those with dementia and anxiety or agitation) selectively received benzodiazepinesduring the earlier time period. Reports of associations between benzodiazepine useand falls led to greater caution, and the apparent association disappeared whenphysicians began to avoid benzodiazepine use in those at high risk of falling.

Therefore, investigators must document the characteristics of the exposedand nonexposed participants and either demonstrate their comparability or usestatistical techniques to adjust for differences. Since investigators cannot recruitgroups that are age-balanced, they must use statistical techniques that correct oradjust for the imbalances.

Effective adjustment for prognostic factors requires the accurate measurementof those prognostic factors. Large administrative databases, while providing asample size that allows ascertainment of rare events, sometimes have limitedquality of data concerning relevant patient characteristics. For example, Jollis andcolleagues20 wondered about the accuracy of information about patient character-istics in an insurance claims database. To investigate this issue, they comparedthe insurance claims data with prospective data collection by a cardiology fellow.They found that a high degree of chance corrected agreement between the fellowand the administrative database for the presence of diabetes: kappa, a measureof chance-corrected agreement, was 0.83 (see Part 2C,Diagnosis, MeasuringAgreement Beyond Chance). They also found a high degree of agreement formyocardial infarction (kappa, 0.76), and moderate agreement for hypertension(kappa, 0.56). However, agreement was poor for heart failure (kappa, 0.39)and very poor for tobacco use (kappa, 0.19). We expand on the limitations of


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administrative databases in another section of this book (see Part 2B,Therapy andHarm, Outcomes of Health Services).

Even if investigators document the comparabil ity of potentially confoundingvariables in exposed and nonexposed cohorts and even if they use statistical tech-

niques to adjust for differences, important prognostic factors that the investigatorsdo not know about or have not measured may be unbalanced between the groupsand, thus, may be responsible for differences in outcome. Returning to our earlierexample, for instance, it may be that the illnesses that require NSAIDs, ratherthan the NSAIDs themselves, are responsible for the increased risk of bleeding.Thus, the strength of inference from a cohort study will always be less than thatof a rigorously conducted RCT.

Case-Control StudiesRare outcomes, or those that take a long time to develop, threaten cohort studiesfeasibil ity. An alternative design relies on the initial identification ofcasesthat is,patients who have already developed the target outcome. The investigators thenchoose controlspersons who, as a group, are reasonably similar to the cases withrespect to important determinants of outcome such as age, sex, and concurrentmedical conditions, but who have not suffered the target outcome. Using thiscase-controldesign, investigators then assess the relative frequency of exposure tothe putative harmful agent in the cases and controls, adjusting for differences inthe known and measured prognostic variables. This design permits the simultane-

ous exploration of multiple exposures that have a possible association with thetarget outcome.

For example, investigators used a case-control design to demonstrate the asso-ciation between diethylstilbestrol (DES) ingestion by pregnant women and thedevelopment of vaginal adenocarcinomas in their daughters many years later.21 AnRCT or prospective cohort study designed to test this cause-and-effect relationshipwould have required at least 20 years from the time when the association was firstsuspected until the completion of the study. Further, given the infrequency of thedisease, either an RCT or a cohort study would have required hundreds of thou-sands of participants. By contrast, using the case-control strategy, the investigatorsdelineated two groups of young women. Those who had suffered the outcome ofinterest (vaginal adenocarcinoma) were designated as the cases (n = 8) and thosewho did not experience the outcome were designated as the controls (n = 32).Then, working backward in time, they determined exposure rates to DES for thetwo groups. The investigators found a strong association between in utero DESexposure and vaginal adenocarcinoma,which was extremely unlikely to be attrib-utable to the play of chance (P < .00001). They found their answer without adelay of 20 years and by studying outcomes in only 40 women.

In another example, investigators used a case-control design relying on com-puter record linkages between health insurance data and a drug plan to investigatethe possible relationship between use of beta-adrenergic agonists and mortalityrates in patients with asthma.22 The database for the study included 95% of thepopulation of the province of Saskatchewan in western Canada. The investigators


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matched 129 cases of fatal or near-fatal asthma with 655 controls who also suf-fered from asthma but who had not had a fatal or near-fatal asthma attack.

The tendency of patients with more severe asthma to use more beta-adrenergicmedications could create a spurious association between drug use and mortality

rate. The investigators attempted to control for the confounding effect of diseaseseverity by measuring the number of hospitalizations in the 24 months prior todeath (cases) or the index date of entry in to the study (control group) and byusing an index of the aggregate use of medications. They found an associationbetween the routine use of large doses of beta-adrenergic agonist metered-doseinhalers and death from asthma (odds ratio [OR], 2.6 per canister per month;95% CI, 1.7-3.9), even after correcting for their measures of disease severity.

As with cohort studies, case-control studies are susceptible to unmeasuredconfounding variables, particularly when exposure varies over time. For instance,

previous hospitalization and medication use may not adequately capture all thevariability in underlying disease severity in asthma. In addition, adverse lifestylebehaviors of asthmatic patients who use large amounts of beta agonists couldcontr ibute to the association. Furthermore, choice of controls may inadvertentlycreate spurious associations. For instance, in a study that examined the associationbetween coffee and pancreatic cancer, the investigators chose control patients fromthe practices of the physicians looking after the patients with pancreatic cancer.23

These control patients had a variety of gastrointestinal problems, some of whichwere exacerbated by coffee ingestion. The control patients had learned to avoid

coffee; as a result, the investigators found an association between coffee (whichthe pancreatic cancer patients consumed at general population levels) and cancer.Subsequent investigations, using more appropriate controls, refuted the associa-tion.24,25 These problems illustrate why clinicians can draw inferences of onlylimited strength from the results of observational studies, even after adjustmentfor known determinants of outcome.

Case Series and Case ReportsCase series(descriptions of a series of patients) and case reports(descriptions ofindividual patients) do not provide any comparison group, and are thereforeunable to satisfy the requirement that treatment and control groups share a similarprognosis. Although descriptive studies occasionally demonstrate dramatic find-ings mandating an immediate change in physician behavior (eg, recall the conse-quences when a link was associated between thalidomide and birth defects26), thereare potentially undesirable consequences when actions are taken in response toweak evidence. Consider the case of the drug Bendectin (a combination of doxyl-amine, pyridoxine, and dicyclomine used as an antiemetic in pregnancy), whosemanufacturer withdrew it from the market as a result of case reports suggestingit was teratogenic.27 Later, even though a number of comparative studies demon-strated the drugs relative safety,28 they could not eradicate the prevailing litigiousatmospherewhich prevented the manufacturer from reintroducing Bendectin.Thus, many pregnant women who potentially could have benefited from thedrugs availability were denied the symptomatic relief it could have offered.


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In general, clinicians should not draw conclusions about cause-and-effectrelationships from case series but, rather, should recognize that the results maygenerate questions for regulatory agencies and clinical investigators to address.

Design IssuesSummaryJust as is true for the resolution of questions of therapeutic effectiveness, cliniciansshould look first for randomized trials to resolve issues of harm. They will often bedisappointed in this search and must make use of studies of weaker design.Regardless of the design, however, they should look for an appropriate controlpopulation before making a strong inference about a putative harmful agent. ForRCTs and cohort studies, the control group should have a similar baseline risk ofoutcome, or investigators should use statistical techniques to adjust or correct fordifferences. Similarly, in case-control studies the derived exposed and nonexposed

groups should be similar with respect to determinants of outcome other than theexposure under study.Alternatively, investigators should use statistical techniquesto adjust for differences. Even when investigators have taken all the appropriatesteps to minimize bias, clinicians should bear in mind that residual differencesbetween groups may always bias the results of observational studies.29 Sinceprescribing in the real world is carried out on the basis of evidence, clinicianvalues, and patient values, exposure opportunities in nonrandomized medicationstudies are likely to differ among patients (channeling bias or effect).

Were Exposed Patients Equally Likely to Be Identif ied in the Tw o Groups?

In case-control studies, ascertainment of the exposure is a key issue. For example,when patients with leukemia are asked about prior exposure to solvents, theymay be more likely to recall exposure than would control group members, eitherbecause of increased patient motivation (recall bias) or because of greater probingby an interviewer (interviewer bias). Clinicians should note whether investigatorsused bias-minimizing strategies such as blinding participants and interviewersto the hypothesis of the study. For example, a case-control study found a twofoldincrease in risk of hip fracture associated with psychotropic drug use. In this study,investigators established drug exposure by examining computerized claims filesof the Michigan Medicaid program, a strategy that avoided both recall and inter-viewer bias.30 The study of beta-adrenergic agonist use in patients with asthmasuggesting an association with mortality also relied on an administrative databaseto ascertain exposure.9 In both cases, the assurance of unbiased exposure statusincreases our confidence in the studies findings.

Were the Outcomes M easured in the Same Way in theGroups Being Compared?

In RCTs and cohort studies, ascertainment of outcome is a key issue. For example,investigators have reported a threefold increase in the risk of malignant melanomain individuals working with radioactive materials. One possible explanation for


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some of the increased risk might be that physicians, aware of a possible risk, searchmore diligently and, therefore, detect disease that might otherwise go unnoticed(or they may detect disease at an earlier point in time). This could result in theexposed cohort having an apparent, but spurious, increase in riska situation we

refer to as surveillance bias.31

Was Follow -up Suff iciently Complete?

As we pointed out in Part 1B1, Therapy, loss to follow-up can introduce biasbecause the patients who are lost may have very different outcomes from those stillavailable for assessment. The longer the required follow-up period, the greater thepossibil ity that the follow-up will be incomplete.

For example, in a well-executed study, investigators determined the vital status

of 1235 of 1261 white males (98%) employed in a chrysotile asbestos textile opera-tion between 1940 and 1975.32 The relative risk for lung cancer death over timeincreased from 1.4 to 18.2 in direct proportion to the cumulative exposure amongasbestos workers with at least 15 years since first exposure. Because the 2% missingdata were unlikely to affect the results, the loss to follow-up does not threaten thevalidity of the inference that asbestos exposure causes lung cancer deaths.


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USING THE GUIDE

R eturning to o ur ea rlier disc uss ion , the study that w e retrieved inves tig ating

the a sso ciation betw een S S RIs and risk of upper gas trointestinal bleeding

used a cas e-control des ign. 6 Data came from a general practitioner electronic

med ical record d atab as e in the United Kingd om , w hich included da ta from

mo re than 3 million people, most o f w hom had been entered pros pectively

during a 5-ye ar period .33-35 The investigato rs ide ntified ca ses of upper ga s-

trointestina l bleeding (n= 1651) an d ulcer perforation (n= 248) am ong pat ients

a ge d 40 to 79 yea rs betw een 1993 and 1997. They then rand om ly s elected

10,000 co ntrols from the a t-risk source po pulation tha t ga ve rise to ca ses ,

choo sing their sam ple so that ag e, sex, and the yea r patients w ere identified

w ere similar am ong the cases and control groups.

The a na lys is co ntrolled fo r a num be r of pos sible prog nos tic facto rs: p revi-

ous dy spe psia, ga stritis, peptic ulcer and upper ga strointestina l bleeding

or perforation , sm oking s tatus, a nd c urrent use o f NS AIDs, an tico ag ulan ts,

co rtico steroids, a nd a spirin. The d ata ba se include d pres cription d rugs o nly.

The investiga tors exa mined the relative freq uency of S S RI prescription use in

the 30 days before the index date(that is, the da te of the reported b leed ing

or perforation ) in patients w ith and w ithout bleeding a nd pe rfora tion a fter

co ntrolling fo r the prog no stic variab les. Co ntrol patients received a ran do m

da te as their index d ate.


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Although the investigators controlled for a number of prognostic factors,

there are other potential impo rtan t determinants o f bleed ing fo r w hich they

did not control. For example, more patients being treated for depression or

anxiety suffer from painful medical conditions than those without depression

an d a nxiety. Patients ma y ha ve b een us ing ove r-the-co unter NS AIDs for these

prob lems . The da taba se the investiga tors used d oes not ca pture the use o f

self-me dication w ith o ver-the-co unter ana lg esics.

Alco hol use is an other po tential co nfound er. Althoug h the inves tig ato rs

excluded patients w ith know n a lcoho lism , ma ny pe rso ns afflicted w ith alco-

holism rema in unrevea led to their prima ry care phy sician , and a lco ho lism

is a sso ciated w ith an increased prevalence of depression and anxiety that

could lead to the prescription of S S RIs. S ince alcoholism is as so ciated w ith

increa se d b lee ding risk, this p rog no stic va ria ble fulfills a ll the c riteria for a

co nfound ing va ria ble that co uld bias the results of the study. Fina lly, it is

pos sible tha t pa tients returning for prescription of S S RIs w ould b e m ore likely

to ha ve their bleeding d iag nos ed in co mpa riso n to pa tients under less intense

surveillan ce (a s tate o f affairs kno w n as detection bias).

Thes e bias es s ho uld a pply to a ll three clas se s o f antide pressa nts (ie,

S S RIs, no nse lective seroton in reuptake inhibitors, and a m isce llan eo us g roup

of othe r drug s) that the investiga tors co nsidered . The results of the study,

w hich w e w ill discuss later in this se ction, sho w ed a n as so ciation only

between gastrointestinal bleeding and SSRIs, rather than between gastroin-

testinal bleed ing a nd o ther antidepressa nt med ications. One w ould expect

all these biase s to influence the as so ciation betw een a ny a ntidepress ant

ag ent and bleeding. Thus, the fact that the investigato rs found the a ss ocia-

tion o nly w ith SS RIs d ecreas es o ur con cern ab out the threats to va lidity

from pos sible d ifferences in prog nos tic fa ctors in those receiving and no t

receiving SSRIs.

At the sa me time, mo st phys icians ma ke d ecisions rega rding the prescrip-

tion of SSRIs or tricyclic antidepressant agents based on particular patient

cha racteristics . Thus, it rema ins pos sible tha t thes e c ha racteristics include

so me that are a sso ciated w ith the incidenc e of g as trointestinal bleeding.

This w ould b e true, for insta nce , if clinicia ns d ifferentially us ed S S RI rathe r

than other antidepressa nt med ications in patients in w hom they suspected

alcohol abuse.

The m ajor streng th of the use o f a larg e da tab as e for this stud y is that it

eliminates the pos sibility o f bias ed as se ss me nt of expo sure (or recall bias )

to S S RIs in the patients w ho s uffered the o utcomes as w ell as in those

w ho d id no t. The outcom es a nd expo sures w ere prob ab ly m eas ured in the

sa me w ay in both g roups, as mo st clinicians are unaw are that UGI bleeding

ma y be a sso ciated w ith SS RI use. We have no idea, how ever, abo ut the

numb er of pa tients los t to follow -up. Althoug h the investiga tors include d


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WHATARE THERESULTS?

How Strong Is the Association Betw een Exposure and Outcome?

We have described the alternatives for expressing the association between theexposure and the outcome, the relative risk and the odds ratio, in other sections ofthis book (see Part 1B1, Therapy ; see also Part 2B2,Therapy and Understandingthe Results, Measures of Association). In a cohort study assessing in-hospitalmortality after noncardiac surgery in male veterans, 23 of 289 patients with ahistory of hypertension died, compared with three of 185 patients without thecondit ion. The relative risk for hypertension and mortality, (23/289)/(3/185), was4.9.36 The relative risk tells us that death after noncardiac surgery occurs almostfive times more often in patients with hypertension than in normotensive patients.

The estimate of relative risk depends on the availability of samples of exposedand unexposed patients, where the proportion of the patients with the outcomeof interest can be determined. The relative risk is therefore not applicable tocase-control studies in which the number of cases and controlsand, therefore,the proportion of individuals with the outcomeis chosen by the investigator.For case-control studies, instead of using a ratio of risks (relative risk), we use aratio of odds (odds ratio): the odds of a case-patient being exposed, divided bythe odds of a control patient being exposed (see Part 2B2,Therapy, Measuresof Association).

When considering both study design and strength of association, we may beready to interpret a small increase in risk as representing a true harmful effectwhen the study design is strong (such as in a RCT). A much higher increase inrisk might be required of weaker designs (such as cohort or case-control studies),as subtle findings are more likely to be caused by the inevitably higher risk of bias.


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only those patients who stayed in the practices of the participating primary

care phys icians from the beg inning to the end o f the study, we do not know ,

for instance , how ma ny people in the datab as e beg an to receive S S RIs but

subs eq uently left those practices.

In sum ma ry, the study suffers from the limitation inherent in a ny o bs erva-

tiona l study: that exposed and unexposed patients ma y differ in prog nos is

at baseline. In this case, at least two unmeasured variables, over-the-counter

NS AID use and alcohol cons umption, m ight c reate a spurious as so ciation

be tw een S S RIs a nd g a strointestinal bleed ing. The o ther ma jor limitation o f

the study is the lack of informa tion reg arding co mpletenes s o f follow -up.

Tha t said, although thes e limitation s w ea ken a ny inferences w e might ma ke,

w e a re likely to conclude that the study is s trong enoug h to w arrant a review

of the res ults.


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Very large values of relative risk or odds ratio represent strong associations thatare less likely to be caused by confounding variables or bias.

In addition to showing a large magnitude of relative risk or odds ratio,a secondfinding will strengthen an inference that we are dealing with a true harmful

effect. If, as the quantity or the duration of exposure to the putative harmful agentincreases, the risk of the adverse outcome also increases (that is, the data suggesta dose-response gradient), we are more likely to be dealing with a causal relation-ship between exposure and outcome. The fact that the risk of dying from lungcancer in male physician smokers increases by 50%, 132%,and 220% for 1 to 14,15 to 24, and 25 or more cigarettes smoked per day, respectively, strengthens ourinference that cigarette smoking causes lung cancer.37

How Precise Is the Estimate of the Risk?Clinicians can evaluate the precision of the estimate of risk by examining theconfidence interval around that estimate (see Part 1B1,Therapy ; see also Part2B2, Therapy and Understanding the Results, Confidence Intervals ). In a studyin which investigators have shown an association between an exposure and anadverse outcome, the lower l imit of the estimate of relative risk associated with theadverse exposure provides a minimal estimate of the strength of the association.By contrast, in a study in which investigators fail to demonstrate an association (anegative study), the upper boundary of the confidence interval around the relative

risk tells the clinician just how big an adverse effect may still be present, despite thefailure to show a statistically significant association (see Part 2B2, Therapy andUnderstanding the Results, Confidence Intervals ).


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USING THE GUIDE

R eturning to o ur earlier discussion, the investiga tors ca lculated od ds ratios

(ORs) of the risk of bleeding in thos e expo sed to S S RIs vs those not expo sed ,

but the y reported the res ults a s rela tive risks (RR). Unfo rtunately, this prac tice

is no t unusual. Fortunately, whe n eve nt rates a re low , relative risks a nd od ds

ratios closely approximate o ne a nother (see Part 2B2, Thera py, Mea sures of

Association ). The investig ato rs found a n as so ciation betw een current use o f

S S RIs a nd upper g as trointes tina l bleeding (ad justed OR, 3.0; 95% CI, 2.1-4.4).

They noted a w ea k as so ciation w ith no nselective s erotonin reuptake inhibitors

(a djusted OR, 1.4; 95% CI, 1.1-1.9), but fo und no as so ciation w ith a ntide pres-

sa nt med ications that had no action o n the se rotonin reuptake m echanism.

The investiga tors found tha t the ass ociation b etw een NSAID use a nd b leed ing

(a djusted OR, 3.7; 95% CI, 3.2-4.4) w a s o f simila r ma g nitude to the as so ciation

betw een b leed ing an d S S RIs. The current use o f SS RIs w ith prescription

NS AID drug s further increa se d the risk of upper ga strointestinal bleeding

(a djusted OR, 15.6; 95% CI, 6.6-36.6). The do se a nd dura tion of S S RI use ha d

little influenc e o n the risk of this ad verse outc om e.


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HOW CAN I APPLY THERESULTSTOPATIENTCARE?

Were the Study Patients Similar to the Patient in M y Pract ice?If possible biases in a study are not sufficient to dismiss the study out of hand, youmust consider the extent to which they might apply to the patient in your office.Is the patient before you similar to those described in the study with respect tomorbidity, age, sex, race, or other potentially important factors? If not, is the biologyof the harmful exposure likely to differ in the patient you are attending (see Part2B3, Therapy and Applying the Results, Applying Results to Individual Patients)?Are there important differences in the treatments or exposures between the patientsyou see and the patients studied? For example, the risk of thrombophlebitis associ-

ated with oral contraceptive use described in the 1970s may not be applicable to thepatient of the 1990s because of the lower estrogen dose in oral contraceptives usedin the 1990s. Similarly, increases in uterine cancer secondary to postmenopausalestrogen replacement do not apply to women who are also taking concomitant prog-estins tailored to produce monthly withdrawal bleeding with chronic,noncyclic use.

Was the Duration of Follow -up Adequate?

Let us return for a moment to the study that showed that workers employed in

chrysotile asbestos textile operation between 1940 and 1975 showed an increasedrisk for lung cancer death, a risk that increased from 1.4 to 18.2 in direct relationto cumulative exposure among asbestos workers with at least 15 years since firstexposure.32 The fact that the follow-up was sufficiently long to capture a largeproportion of the lung cancers destined to occur enhances our confidence inapplication of the results to patients in our practice. By contrast, excessively shortfollow-up may fail to detect harmful effects that emerge with longer observation.

What Was the M agnitude of the Risk?The relative risk and the odds ratio do not tell us how frequently the problemoccurs; they tell us only that the observed effect occurs more or less often in theexposed group compared to the unexposed group. Thus, we need a methodfor assessing clinical importance. In our discussion of therapy (see Part 1B1,Therapy ; see also Part 2B2,Therapy and Understanding the Results, Measuresof Association), we described the way to calculate the number of patients whomust be treated to prevent an adverse event. When the issue is harm, we can usedata from a randomized trial or cohort study, but not a case-control study, tomake an analogous calculation to determine how many people must be exposedto the harmful agent to cause an adverse outcome.

For example, over an average of 10 months of follow-up, investigators conduct-ing the Cardiac Arrhythmia Suppression Trial (CAST), a RCT of antiarrhythmicagents,38,39 found that the mortality rate was 3.0% for placebo-treated patients and


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clinical conditions. Depending on both their safety profile after longer experienceand cost-effectiveness considerations, COX 2-inhibiting NSAIDs may prove tobe an appropriate alternative class of agents.

CLINICALRESOLUTION

To decide on your course of action, you proceed through the three steps of usingthe medical literature to guide your clinical practice. First, you consider thevalidity of the study before you. The antidepressant and upper gastrointestinalbleeding study addressed multiple classes of antidepressant agents and the risk ofupper gastrointestinal bleeding or ulcer perforation.You decide that the limita-

tions of the case-control design, along with the lack of information about loss tofollow-up, leave you uncertain about a causal relationship between SSRIs andgastrointestinal bleeding. Furthermore, this is a single study and, as we have previ-ously mentioned, in other areas of medicine subsequent investigations11,12, 42-45havefailed to confirm many apparent harmful associations.10,46, 47

Turning to the results, you note the very strong association between the com-bined use of SSRIs and NSAIDs. Despite the methodologic limitations of thissingle study,you believe the association is too strong to ignore.You thereforeproceed to the third step and consider the implications of the results for the

patient before you.The primary care database from which the investigators drew their sample

suggests that the results are readily applicable to the patient before you. You con-sider the magnitude of the risk to which you would be exposing this patient ifyou prescribed an SSRI and it actually did cause bleeding. Using the baseline riskreported by Carson et al in a similar population,14 you calculate that you wouldneed to treat about 625 patients with SSRIs for a year to cause a single bleedingepisode in patients not using NSAIDs, and about 55 patients a year taking NSAIDsalong with an SSRI for a year to cause a single bleeding episode.

From previous experience with the patient before you, you know that he isrisk averse. When he returns to your office, you note the equal effectiveness of theSSRIs and tricyclic antidepressants that you can offer him, and you describe theside-effect profi le of the alternative agents.You note, among the other considera-tions, the possible increased risk of gastrointestinal bleeding with the SSRIs. Thepatient decides that, on balance, he would prefer a tricyclic antidepressant andleaves your office with a prescription for nortriptyline.


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