AMERICAN JOURNAL OF EPIDEMIOLOGYCopyright © 1985 by The John* Hopkins University School of Hygiene and Public HealthAll rights reserved

VoL 122, No. 3Printed in U.SJi.

CONFOUNDING AND MISCLASSIFICATION

SANDER GREENLAND1-3 AND JAMES M. ROBINS1

Greenland, S. (UCLA School of Public Health, Los Angeles, CA 90024), and J.M. Robins. Confounding and misdassfflcation. Am J Epidemiol 1985; 122:495-506.

The authors examine some recently proposed criteria for determining when toadjust for covariates related to mlsdassification, and show these criteria to beincorrect In particular, they show that when misdassffication is present, covariatecontrol can sometimes increase net bias, even when the covariate would havebeen a confounder under perfect classification, and even if the covariate is adeterminant of classification. Thus, bias due to misclasstflcation cannot beadequately dealt with by the methods used for control of confounding. Theexamples presented also show that the "change-in-estimate" criterion for decid-ing whether to control a covariate can be systematically misleading when mis-classification is present These results demonstrate that it is necessary toconsider the degree of misdassiflcation when deciding whether to control acovariate.

biometry; epkJemiologic methods

Most epidemiologic studies are designedto estimate the effect of some exposurefactor (or factors) on the risk of a particulardisease. Despite considerable research, theissue of when adjustment for a covariate isnecessary in this process remains contro-versial. Some recent works (1-3) have ex-plicitly or implicitly put forth recommen-dations regarding adjustment when selec-tion bias or misclassification is present inthe study. Each of these works dealt withsituations in which the covariates weretreated as confounders, i.e., variables forwhich adjustment was necessary to removebias in the estimator of effect. The purposeof this paper is to critically examine somerecent recommendations regarding adjust -

Received for publication March 8,1984 and in finalform February 20, 1985.

Abbreviation: SMR, standardized morbidity ratio.1 Division of Epidemiology, UCLA School of Public

Health, Los Angeles, CA 90024.• Occupational Health Program, Harvard School of

Public Health, Boston, MA.' Partially supported by NCI grant RO-CA-16042.The authors thank James Schlesselman and Alex-

ander Walker for their helpful comments.

ment for covariates related to classification,and to offer some alternative recommen-dations.

Current writings on confounding (1-4)suggest that if no other biases are presentthe following conditions are necessary fora covariate to be a confounder 1) it mustbe a predictor of risk among the unexposed;2) it must be a correlate of exposure in thepopulation serving as the source of subjects;and 3) it should not be an intermediatevariable in the causal pathway under study.Figure la illustrates these criteria in a pathdiagram.

In case-control studies, the preceding cri-teria can be broadened to allow adjustmentfor certain types of selection bias. Day etal. (1) note that if the covariate is a riskpredictor but not a correlate of exposure inthe source population (figure lb), control-ling it may still reduce bias if the covariateinfluences selection differentially with re-spect to exposure. And Miettinen and Cook(3) note that if the covariate is a correlateof exposure but not a risk predictor (figurelc), controlling it may still reduce bias if

495

496 GREENLAND AND ROBINS

b) F -

d) F-

f) F-

C C

FIGURE 1. Path diagrams illustrating causal structures in source populations.

the covariate influences selection differen-tially with respect to disease status. Unfor-tunately, other authors have inappro-priately extended these principles to situa-tions in which the covariate is an interme-diate variable (figure Id) or a consequenceof exposure and disease (figure le) (5). Insuch situations, there may indeed be selec-tion bias due to the covariate, but adjust-ment for the covariate may produce a biaseven more severe than the original selectionbias (6). Thus, not all forms of selectionbias can be regarded as confounding or beadequately dealt with by covariate control.

Some authors have suggested extensionsof the above principles to situations involv-ing misclassification of exposure or disease(2, 3). We will argue below that several ofthe extensions that have been proposed areincorrect. In particular, the counterexam-ples we will present will show that adjust-ment for a determinant of classification canaggravate bias.

The examples will concern epidemiologicstudies of the effect of an exposure factorF (F = 1, present; F = 0, absent) on risk ofa disease outcome D (D = 1, disease occurs;D = 0, disease does not occur) over a fixedrisk period in a well-defined population.The covariate will be denoted C (C = 1,present; C = 0, absent). The effect of F will

be defined in terms of the rate ratio, esti-mated from case-control studies by theodds ratio. The disease will be assumed tobe "rare" over the study period to avoiddistinctions that arise in the general case.Nevertheless, all that follows applies tomore general settings involving commondiseases, multilevel factors, and measuresof association other than the rate ratio andodds ratio.

"Expected values" will be taken to belarge-sample expectations. Critical in whatfollows will be the idea of "net bias," de-fined for present purposes as the differencebetween the true effect parameter and theexpected value of the chosen estimator.

(The definition of a confounder is notwell agreed upon in settings in which thetrue effect parameter cannot be unbiasedlyestimated from the observed data on F, C,and D. One might continue to define C tobe a confounder only under the above con-ditions. Instead, in this paper, we will de-fine C to be a confounder if the net bias ofthe crude estimator exceeds that of theadjusted estimator, regardless of conditions1) and 2) above. As shown below, in theabsence of information on misclassificationrates, it is often impossible to determinefrom the data either the validity of condi-tions 1) and 2) or the relative bias of thecrude and adjusted estimators.)

CONFOUNDING AND MISCLASSIFICATION 497

COVARIATES UNRELATED TO

CLASSIFICATION

Consider a situation in which the covar-iate is associated with exposure but not arisk predictor (as in figures lc or If). It hasbeen suggested that the situation shown infigure If "may lead to genuine confoundingwhen the variables are measured with er-ror" (2, p. 106) and the following examplewas used to illustrate this assertion.

Example 1

Suppose that the underlying source pop-ulation structure is as in table 1. A case-control study taking all cases and an equalnumber of controls, but nondifferentiallymisclassifying F 10 per cent of the time(i.e., sensitivity and specificity for measure-ment of F equals 0.9 across all levels of Cand D) will have expected data as in table2, where F* = 1 for subjects classified as UFpresent" and F* = 0 for subjects classifiedas UF absent." (To illustrate the construc-tion of table 2, note that the upper lefthand cell of table 2 is 0.9 (90) + 0.1 (1) =

TABLE 1

Source population structure for examples 1 and 2

Expected no. ofincident cases

Population atrisk

Rate ratioparameters

C

F-l

90

9,000

= 1

F = 0

1

10,000

100

C - 0

F-l F-0

10 9

1,000 90,000

100

Crude rate ratio parameter, 100.

TABLE 2

Expected data for example 1 (case-control study ofpopulation in table 1 with sensitivity and specificity ofmeasurement of F having constant sensitivity = 0.90

and specificity = 0.90)

CasesControls

Expected oddratio*

f* =

819

C - 1

1 F

9

1010

0 F- -

1010

C -

1

9

0

F*-0

981

Expected crude odds ratio, 23.F*, measured value of F.

81 when rounded to the nearest whole num-ber.) We can see from table 1 that, in theabsence of other biases, the true effect cor-responds to a rate ratio of 100. In contrast,the expected crude rate ratio estimate fromthe study (table 2) is 23, but the expectedadjusted rate ratio estimate is 9, even morebiased.

Contrary to the implication of the quotecited above, it is evident that adjustmentfor the covariate in example 1 dramaticallyincreases the net bias, rather than reducesit. Thus, the covariate is not a genuineconfounder in this situation. The examplealso demonstrates the pitfall of using theobserved study data to judge whether con-founding is present: misclassification caneasily distort the apparent degree of con-founding or effect modification by a thirdvariable. This point has been made beforeby one of the present authors (7).

Example 1 turns out to be an illustrationof a more general feature of nondifferentialmisclassification of exposure (proven in theAppendix): if the odds ratios are constantacross strata, the covariate is associatedwith exposure but not classification or dis-ease, and sensitivity and specificity sum tomore than 1.0, then the misclassificationbias in the standardized odds ratio will begreater than that in the crude (unless thereis no association of exposure with disease,in which case neither estimate will bebiased). As discussed in the Appendix, thistheorem extends to cohort studies. Thetheorem also extends to case-control stud-ies of populations in which the disease(rather than exposure) is nondifferentiallymisclassified and the covariate is associatedwith disease (instead of exposure). If, how-ever, only one of exposure and disease aremisclassified, the misclassification is non-differential, and the covariate is associatedonly with the correctly classified variable,then both the standardized and crude oddsratios will be equally biased towards thenull (this follows directly from a theoremof Korn (8)); furthermore, nondifferentialmisclassification of a nonconfounding co-

498 GREENLAND AND ROBINS

variate will produce no bias in either thestandardized or crude odds ratio.

In example 1, nondifferential misclassi-fication of the exposure generated the spu-rious appearance of confounding by a co-variate (in the sense that the crude andadjusted values differ), and nondifferentialmisclassification of the disease can do so aswell. As the following example shows, dif-ferential misclassification of a noncon-founding covariate can also generate thespurious appearance of confounding.

Example 2

Consider again the case-control study ofthe source population described in example1 and table 1, but with C rather than Fmeasured with error. Specifically, supposethe presence of C is detected with perfectspecificity but with a sensitivity of 0.98among cases and 0.90 among noncases (asmight occur, for example, if the covariaterepresented an event for which the caseshad better recall). The expected data wouldthen be as in table 3. The expected crudeodds ratio differs from the expected stan-dardized morbidity ratio (SMR) estimate(9, 10) and the expected Mantel-Haenszelestimate (2, 4), yet it is the crude (ratherthan any adjusted value) that equals thecorrect population rate ratio. This occursfor two reasons: first, since F and D are notmisclassified, the expected crude odds ratioequals the crude rate ratio parameters, andsecond, the crude parameter equals the

TABLE 3

Expected data for example 2 (case-txntrol study ofpopulation in table 1 with differential misclassification

of C: sensitivity = 0.98 among cases and 0.90 amongcontrols, specificity = 1.00 in both groups)

CasesControls

Expected oddsratios

C -

F-l

888

99

1

F = 019

C*-

F = l

122

61

• 0

F - 0

991

stratum-specific values. (The misclassifi-cation has also generated a spurious ap-pearance of odds ratio heterogeneity.)

PREDICTORS OF EXPOSURECLASSIFICATION

It has been suggested that in case-controlstudies "study procedures that bear on theaccuracy of information on exposure... areconfounders if they are distributed differ-ently between the index (case) and refer-ence [control] series" (3, p. 598). The fol-lowing example shows that this claim isfalse as a general principle.

Example 3

Suppose the correctly classified expecteddata in a case-control study are as given intable 4, and that these numbers perfectlyreflect the magnitude of the effect of thestudy factor on incidence. Let C = 1 indi-cate that the exposure information was ob-tained by direct interview with subject, andC = 0 that the subject had died before aninterview could be performed (so informa-tion was obtained from next-of-kin). Notethat a higher proportion of controls weredirectly interviewed. Suppose that inter-views of next-of-kin of deceased subjects(C = 0) always had a sensitivity (for expo-sure) of 0.75 and a specificity of 0.85, whiledirect interviews of subjects (C = 1) alwayshad a sensitivity of 0.90 and a specificity of0.95. The expected misclassified data wouldthen be as in table 5; we see that the crudeodds ratio is 1.8, closer to the correct valueof 2 than any of the adjusted or stratum-specific values. Thus, adjustment for the

TABLE 4

Expected correctly classified data for example 3.(C •= 1 if subject directly interviewed,

C-0 otherwise.)

Expected crude odds ratio, 100.Expected SMR estimate (9,10), 92.Expected Mantel-Haenszel odds ratio (2, 4, 18), 73.C*, measured value of C.

CasesControls

Correct oddsratios

C - 1

F-*l F-0

20 80100 800

2.00

C - 0

F - l F = 0

120 48040 320

2.00

Correct crude odds ratio, 2.00.

CONFOUNDING AND MISCLASSIFICATION 499

TABLE 5

Expected data under misclassification, example 3(case-control study of subjects in table 4, with C a

determinant of exposure classification: sensitivity =0.90 and specificity = 0.95 when C = 1, sensitivity =

0.75 and specificity = 0.85 when C = 0)

CasesControls

Expected oddsratios

C - l

F*-l F* = 0

22 78130 770

1.67

F* =

16278

C - 0

1 F* = 0

438282

1.34

Expected crude odds ratio, 1.80.Expected SMR estimate, 1.37.Expected Mantel-Haenszel odds ratio, 1.39.F*, measured value of F.Expected crude odds ratio under matching on

C, 1.37.

source of information is unnecessary in thisexample, and in fact harmful in that itincreases net bias.

Suppose in the above example one hadmatched the controls to cases on source ofinformation (C), so the same proportion ofcontrols as cases (14 per cent) had beendirectly interviewed. The expected adjustedodds ratios would then be about the sameas before, but the expected crude odds ratiowould now be only 1.4. Thus, matching onsource of information would also be harm-ful in this example.

Note that the covariate in example 3 wasnot actually related to the exposure withineither the case series or the control series(table 4). Thus, a covariate need not berelated to the exposure in order to spu-riously mimic a confounder through its ef-fects on exposure classification. Example 1illustrates that if a covariate is related toexposure, it need not be related to diseaseor classification in order to spuriouslymimic a confounder.

Example 3 illustrates a failure of the oft-repeated validity criterion of comparabilityof measurement (11, 12): in the example,focusing the analysis within groupingsbased on measurement comparability led toless valid results than simple pooling ofsubjects without regard to measurementcomparability. Even restriction of the anal-ysis to the subjects with the most accurate

measurements (stratum C = 1) producedless valid results than a crude analysis ofall subjects. Nevertheless, this comparabil-ity criterion may have its origin in examplessuch as the following, which parallels ex-ample 3 yet illustrates a general situationin which adjustment for a determinant ofexposure classification reduces bias.

Example 4

Suppose the correctly classified expecteddata in a case-control study are as given intable 6, and that these numbers perfectlyreflect the magnitude of the effect of thestudy factor on incidence (note in particu-lar that there is no effect). Let C be definedas in example 3, and the sensitivities andspecificities within levels of C be as in ex-ample 3. The expected misclassified datawould then be as in table 7. We see thatthe crude odds ratio is biased away fromthe correct value of 1.00, whereas the strat-ified odds ratios are not. Thus, in this ex-ample, adjustment for the source of infor-mation (indicated by C) is essential forvalidity.

TABLE 6

Expected correctly classified data for example 4

Expected no. ofincident cases

Population at risk

Correct oddsratios

C

F - 1

10100

- 1

F-0

80800

1.00

C - 0

F-1 F-0

60 48040 320

1.00

Correct crude odds ratio, 1.00.

TABLE 7

Expected data under misclassification, example 4(case-control study of subjects in table 6, with C a

determinant of exposure classification: sameclassification rates as example 3)

CasesControls

Expected oddsratios

I

F*-

13130

C-l

1 F'-O

77770

1.00

f -

11778

C = 0

1 F*-0

423282

1.00

Expected crude odds ratio, 1.32.F*, measured value of F.

500 GREENLAND AND ROBINS

The effect of covariate adjustment on netbias in example 4 was opposite to that inexample 3. Consequently, one cannot statethat in general a predictor of exposure clas-sification should or should not be treatedas a confounder. Nevertheless, example 4illustrates a general principle of hypothesistesting: suppose that no other biases arepresent, and within levels of the covariatemisclassification of exposure is nondiffer-ential and there is no true exposure-diseaseassociation; then the true large-sample al-pha level (type I error rate) of any of theusual stratified tests of association (e.g.,Mantel-Haenszel (4)) will not exceed theirnominal alpha-level (8). And (except forsome special cases of unusual structure) ifthe covariate is both a predictor of the(nondifferential) exposure classification er-rors and associated with disease, stratifi-cation on the covariate will be necessary toproduce a test of size within the nominalalpha-level (this is because exposure will bedifferentially misclassified within the crudetable). "Comparability of measurement"therefore remains a valid criterion for hy-pothesis testing. Although forcing "com-parability of measurement" also guaranteesthat the measurement bias in point esti-mation will be towards the null, example 3demonstrates that the net bias can some-times be greatly increased by such action.

PREDICTORS OF DIAGNOSTIC ERROR

Misclassification of disease status is of-ten referred to as misdiagnosis or diagnos-tic error. It has been stated that confoun-ders "are predictors (determinants) of di-agnosing the illness—by being either riskindicators or determinants of diagnostic er-rors—in the type of setting represented bythe study" (3, p. 594). The following ex-ample shows that (contrary to the preced-ing quote) a determinant of diagnostic errormay be associated with the study factor andyet not be a true confounder.

Example 5

Suppose our source population is actuallyas in table 8 (showing a true effect param-

eter of rate ratio = 2.00 and an associationof C with F), and C is a determinant ofdiagnostic errors as shown in the table: inthe population with C present, diagnosis ofdisease takes place with a 95 per cent sen-sitivity and a 0.08 per cent false positiverate over the study period, while in thepopulation with C absent, diagnosis of dis-ease takes place with 90 per cent sensitivityand 0.06 per cent false positive rate. If wedo a follow-up study of the entire popula-tion and expend no additional case-findingor case-screening efforts, our expected datawill be as in table 9: the expected crude rateratio estimate is 1.67, while the expectedadjusted estimates are around 1.56. Thus,adjustment for the determinant of diagnos-tic error is unnecessary in this example,and in fact harmful in that it increases netbias. As in the last two examples, the ad-justed estimators are more biased than thecrude, so that, despite its association withexposure and its influence on diagnosticerrors, the covariate is not a true con-founder. Note also that adjustment for thecovariate would produce bias in a case-control study of this population.

The belief that pure determinants of di-agnosis should be treated as confoundersmay have its origin in examples such as thefollowing, which parallels example 5 yetillustrates a general situation in which ad-justment for a determinant of diagnosticerror reduces bias.

Example 6

Suppose the source population structurewas as in table 10, with C a determinant ofdiagnostic errors as shown: F and C havethe same association as in example 5, andthe sensitivity and false positive rate ofdisease diagnosis is also the same as inexample 5. The only difference is that, un-like in example 5, F has no effect. If we doa follow-up study of the entire populationand take as cases all and only those diag-nosed as such, our expected data will be asin table 11. We see that the crude rate ratiois biased away from the correct value of

CONFOUNDING AND MISCLASSIFICATION 5 0 1

TABLE 8

Source population structure for example 5

Expected no. ofDiagnosed casesUndiagnosed cases

Expected no. of noncases diagnosedas cases

Population at risk

True rate ratio parameters (based ontrue cases only)

F - 1

764

32

40,000

C o l

F = 0

191

16

20,000

2.00

F-1

328

12

20,000

C - 0

F-0

328

24

40,000

2.00

Apparent casesPopulation at risk

Expected rateratio estimates

C

F = 1

10840,000

- 1

F-0

3520,000

1.54

C

F = 1

4420,000

- 0

F-0

5640,000

1.57

Crude rate ratio parameter (based on true cases only), 2.00.

TABLE 9 The effect of covariate adjustment on netExpected data for example 5 (follow-up study of bias in example 6 was opposite to that in

population in table 8 using aUdiagnos&l persons as e x a m p l e g. Therefore, One cannot state thatcases, C a determinant of disease diagnosis) , .. . . .

in general a predictor of diagnostic errorsshould or should not be treated as a con-founder. Nevertheless, example 6 illus-trates a general principle parallel to the onegiven after example 4: suppose that noother biases are present, and within covar-

Expected crude rate ratio ertimate, i.67. iate levels there is no tnie exposure-diseaseExpected SMR estimate, 1.66. association and diagnostic errors are non-Expected Mantei-Haenszei rate ratio ertimat., 1.56. differential; then the true large-sample al-

pha level of any of the usual stratified testsof association will not exceed their nominal

1.00 (albeit slightly), whereas the stratified alpha-level (8). And (except for some spe-rate ratios are not. Thus, in this example, cial cases of unusual structure) if the co-adjustment for the diagnostic predictor was variate is both a predictor of the (nondif-appropriate for validity. ferential) diagnostic errors and associated

TABLE 10

Source population structure for example 6

Expected no. ofDiagnosed casesUndiagnosed cases

Expected no. of noncasesdiagnosed as cases

Population at risk

True rate ratio parameters(based on true cases only)

C - 1

F-1

382

32

40,000

1.00

F-0

191

16

20,000

F-1

182

12

20,000

C - 0

F-0

364

24

40,000

1.00

Crude rate ratio parameter (based on true cases only), 1.00.

502 GREENLAND AND ROBINS

TABLE 11

Expected data for example 6 (follow-up study forpopulation in table 10 using all diagnosed persons as

cases, C a determinant of disease diagnosis)

Apparent casesPopulation at risk

Expected rateratio estimate*

C

F- 1

7040,000

= 1

F-0

3620,000

1.00

C

F - 1

3020,000

= 0

F - 0

6040,000

1.00

Expected crude rate ratio estimate, 1.06.

with the exposure, stratification on the co-variate will be necessary to produce a testof size within the nominal alpha-level(again, because the diagnostic errors will bedifferential within the crude table). Predic-tors of diagnostic accuracy may thus betreated as confounders in hypothesis test-ing. But example 5 demonstrates that con-trol of such predictors can sometimesgreatly increase net bias in point estima-tion.

IMPLICATIONS FOR THE CONTROL OFMISCLASSIFICATION BIAS

The above examples show that, despiteconjectures to the contrary, predictors ofclassification or diagnosis cannot be ade-quately dealt with in the same frameworkas predictors of risk. In particular, a co-variate can be a determinant of exposureclassification or disease diagnosis but itmay nevertheless be detrimental to adjustfor the covariate. This appears to runcounter to usual epidemiologic intuitions(cf., 11, 12), and yet the above examplesought to be sufficient to rule out a simpleparallelism between confounder controland misclassification control. Furthermore,the misclassification rates employed aboveare not numerically extreme, making itdoubtful that the hoped-for parallelismmight hold approximately: for example,Copeland et al. (13, table 2) reviewed re-ported sensitivities and specificities ofseven measurements and found four in-stances in which sensitivity was below 60per cent or specificity was below 75 percent. More recent studies have found under80 per cent agreement between interview

responses and medical records for certaintypes of drug history items (14-16) (lowagreement necessarily implies high errorrates for one or both of the sources); differ-ential recall was indicated in some in-stances (16). Even when the error ratesappear "low," errors can produce sizeabledistortions if the presence or absence of theexposure or disease is "rare" (as in example4 or the real data reported by Schulz et al.(17)).

This leaves three strategies for the con-trol of misclassification bias: 1) preventionof misclassification through improvedmeasurement methods; 2) algebraic correc-tion for misclassification (which requires asource of error-rate estimates, such as avalidation substudy); and 3) control ofthose covariates for which control could beargued to reduce misclassification bias inthe specific analysis being performed. Thefirst two strategies have been extensivelydiscussed in a number of recent publica-tions (e.g., 13, 17-20), while the third ap-pears to have been either ignored or mis-perceived. With regard to the third strat-egy, a general principle was illustrated byexamples 3-6: if misclassification is non-differential within levels of a covariate butvaries across levels of the covariate, then,in the absence of other sources of bias,control for the covariate will in generalimprove the validity of the test of associa-tion of factor and disease; nevertheless,control of the covariate may in some in-stances increase the net bias in estimation(cf., example 3, 5). In this case, the soleadvantage of the adjusted point estimate isthat the direction of its misclassificationbias is known a priori (i.e., it is towards thenull); if the misclassification is differential,however, this advantage is lost.

IMPLICATIONS FOR IDENTIFICATION OF

CONFOUNDING

The above examples also show how studydata can be systematically deceptive as towhether or not a covariate is a confounder(in the sense of requiring control). For ex-

CONFOUNDING AND MISCLASSIFICATION 503

ample, it may be known a priori that thecovariate is associated with exposure whileits status as a risk predictor may be un-known (or vice versa). In such situationsthe data are usually employed to decidewhether or not the covariate is a con-founder by comparing the crude and ad-justed estimates; the latter is chosen if thetwo differ to an important extent. Evenassuming no misclassification is present,this "change-in-estimate" criterion is prob-lematic (3, 21); when misclassification ispresent (as it almost always is), the criter-ion may lead to unnecessary and even bias-producing control of the covariate (as inexamples 1-3 and 5).

It follows that accuracy of confounderidentification will benefit from applicationof the above three strategies for control ofmisclassification bias; the problems dis-cussed here will not arise if misclassifica-tion is prevented; confounding should beevaluated after application of correctionsfor misclassification; and if control of acovariate can be argued to reduce misclas-sification bias, the rationale for controllingit no longer depends on whether it has boththe associations depicted in figure la.

This still leaves situations in which boththe degree of misclassification and the de-gree of covariate-exposure or covariate-dis-ease association are unknown. Example 1provides an extreme illustration of theproblem: in actual practice, we would onlyobserve the study data (table 2), whichshow a marked difference between thecrude and adjusted estimates. If we attrib-uted most of this difference to confoundingby the covariate we should prefer the ad-justed estimate, but if we attributed mostof it to nondifferential misclassification ofthe study factor we should prefer the crudeestimate. And if we were uncertain aboutthe relative strength of each source of bias,we should be correspondingly uncertainabout which estimate to prefer.

There are several informal ways of cop-ing with this dilemma. The simplest is topresent both the crude and adjusted results,

along with some arguments bearing onwhich is likely to be the more accurate ofthe two. A related approach is to computeconfidence limits with and without con-trolling the covariate in question, and thenbase inference on an interval composed ofthe smallest lower limit and the largestupper limit. The interval so constructedshould cover the true parameter at least atthe nominal coverage rate if at least one ofthe crude and adjusted analyses is un-biased, or if the analyses are biased in op-posite directions. If both analyses arebiased in the same direction, the compositeinterval will still cover the true parameterno less than the better of the two originalintervals.

The "composite interval" approach canbe extended to deal with situations involv-ing several sources of uncertainty in theanalysis: one can compute limits control-ling for various covariate subsets, or afterapplying corrections for misclassificationbased on various assumptions about theerror rates; one then constructs the com-posite interval from the minimum of theset of lower limits and maximum of the setof upper limits so obtained. The obviousdisadvantage of the resulting interval is itspotentially extreme conservatism, as re-flected by excessive width. Although a widecomposite interval may in a rough senseproperly reflect the degree of uncertaintyin the results, we caution that we regardsuch intervals as an informal aid to studyinterpretation rather than a substitute forestablished statistical methods.

DISCUSSION

Most of the literature has not consideredthe combined effects of the various biases,for the good reason that the number ofspecial situations to consider is enormous.There are, however, examples showing thatmisclassification can reduce one's ability tocontrol confounding (7) and that (legiti-mate) strategies for confounder control canincrease misclassification bias (22). Morecomplex situations can be envisioned: con-

504 GREENLAND AND ROBINS

sider, for example, a matched-pair case-control study in which a confounder is usedas a matching factor but is routinely mis-classified during selection, resulting in theselection of mismatched controls. As a con-sequence, either the study results will re-main confounded by the confounder or, ifthe confounder is correctly measured in theanalysis, many of the subjects will be leftunmatched; loss of validity or efficiency isthus inevitable in this situation.

In most epidemiologic studies, all sourcesof bias will variously cancel and interact ina manner too complex for accurate analysis.It is perhaps for this reason that someauthors criticize overemphasis of formalstatistical results in drawing and present-ing conclusions from epidemiologic data.But granting that formal methods do notadequately address these problems, numer-ical reasoning can still be employed to eval-uate the likely impact of various sources ofbiases on the study data at hand, and tocheck on the validity of any general rec-ommendations that appear in the methodo-logic literature.

We have seen that misclassification bias(including biases arising from diagnosticerrors) cannot in general be controlled bythe same basic methods used to controlconfounding or some forms of selectionbias. If we have accurate estimates of theclassification probabilities, corrections formisclassification are possible (13, 18-20,22). Nevertheless, the true classificationrates are virtually never known, and esti-mates of them will usually be subject toconsiderable error so that the "corrected"estimates will not be fully corrected formisclassification bias. It is also known thatrelatively modest degrees of misclassifica-tion can produce large amounts of bias (7,13, 22). These observations taken togetherindicate that, similarly to many other prob-lems, prevention of misclassification bias issuperior to any analytic cure.

The contingency-table results presentedhere and elsewhere (7, 8, 13, 18, 22) haveimmediate consequences for binary regres-

sion methods, such as logistic regression.Most importantly, we note that misclassi-fication of a regressor can bias the coeffi-cient estimates for other regressors, even ifthe misclassification is nondifferential (cf.,example 1) or even if the true coefficient ofthe misclassified regressor is zero (cf., ex-ample 2); misclassification of a regressorcan also bias interaction estimates (cf., ex-amples 2 and 3, and reference 7). Theseobservations point out the necessity of con-sidering the measurement quality of allvariables entered in a model, even whenonly certain effects within the model arethe object of study. Similar conclusionshave been reached by Kupper (23) in thecase of ordinary regression. Examples 3 and5 also imply that the addition of "dataquality" indicators to models (such as avariable indicating whether data were ob-tained from the subject or from a surrogate(24)) can sometimes increase bias in someor all of the risk factor coefficients.

REFERENCES

1. Day NE, Byar DP, Green SB. Overadjustment incase-control studies. Am J Epidemiol 1980;112:696-706.

2. Breslow NE, Day NE. Statistical methods in can-cer research. Volume 1. The analysis of case-control studies. IARC Scientific Publication No.32. Lyon: International Agency for Research onCancer, 1980.

3. Miettinen OS, Cook EF. Confounding: essenceand detection. Am J Epidemiol 1981;114:593-603.

4. Schlesselman JJ. Case-control studies: design,conduct, analysis. New York: Oxford UniversityPress, 1982.

5. Horwitz RI, Feinstein AR. Alternative analyticmethods for case-control studies of estrogen andendometrial cancer. N Engl J Med 1978;299:1980-94.

6. Greenland S, Neutra RR. An analysis of detectionbias and proposed corrections in the study ofestrogens and endometrial cancer. J Chronic Dis1981;34:433-8.

7. Greenland S. The effect of misclassification in thepresence of covariates. Am J Epidemiol 1980;112:564-9.

8. Korn EL. Hierarchical log-linear models not pre-served by classification error. J Am Stat Assoc1981;76:110-13.

9. Miettinen OS. Standardization of risk ratios. AmJ Epidemiol 1972^6:383-8.

10. Greenland S. Interpretation and estimation ofsummary ratios under heterogeneity. Stat Med1982;l:217-27.

CONFOUNDING AND MISCLASSIFICATION 505

11. MacMahon B, Pugh TF. Epidemiology: principles 18. Kleinbaum DG, Kupper LL, Morgenstern H. Ep-and methods. Boston: Little, Brown, 1970. idemiologic research: principles and quantitative

12. Miettinen OS. The "case-control" study: valid se- methods. Belmont, CA: Lifetime Learning, 1982.lection of subjects. J Chronic Dis 1985 (in press). 19- Fleiss JL. Statistical methods for rates and pro-

13. Copeland KT, Checkoway H, McMichael AJ, et portions. 2nd ed. New York: John Wiley and Sons,aL Bias due to misclassification in the estimation 1981.of relative risk. Am J Epidemiol 1977;105:488-95. w- Greenland S, Kleinbaum DG. Correcting for mis-

14. Brody DS. An analysis of patient recall of their classification in two-way tables and matched-pairpast therapeutic regimens. J Chronic Dis O1 Btuies. IntJ Epidemiol 1983;12^3-7.1980-33-57-63 Robins J, Morgenstern H. Confounding and prior

15. Paganini-HillA, Ross RK. Reliability of drug n&Ox**' {AbStmCt)- ** J EPidemio1 1 9 8 3 ;

£ * f " ^ a o ^Tn***infonnation- ^ J 22. Greenland S. The effect of misclassification inEpidemiol 1982;116:114-22 matched-pair case-control studies. Am J Epide-

16. Rosenberg MJ, Layde PM, Ory HW, et al. Agree- ^ j i982;116:402-6.ment between women's histories of oral contra- 23. Kupper LL. Effects of the use of unreliable sur-ceptive use and physician records. Int J Epidemiol I0geLte variables on the validity of epidemiologic1983;12:84-7. research studies. Am J Epidemiol 1984;12(h643-8.

17. Schulz KF, Cates W, Grimes DA, et aL Reducing 24. Pickle LW, Greene MH, Ziegler RG, et al. Colo-classification errors in cohort studies. Stat Med rectal cancer in rural Nebraska. Cancer Res1983;2:25-31. 1984;44:363-9.

APPENDIX

Proof of theorem corresponding to example 1Suppose a covariate is associated with exposure but not associated with classification or the disease, the

exposure is nondifferentially misclassified with sensitivity Q and specificity P (and P + Q > 1), and the truestratum-specific odds ratio R for the exposure-disease association is constant across the covariate levels. Thenthe misclassification bias in the standardized morbidity ratio (SMR) estimate ("internally" standardized oddsratio, weighting the odds ratios based on the covariate distribution in the exposed controls) (9, 10) will begreater than the misclassification bias in the crude odds ratio (unless R •» 1, in which case neither are biased).In particular, if SMR and Rc represent the large-sample expectations of the standardized and crude estimators,we have that R < 1 impliesR<RC< SMR< 1 and R > 1 implies ft > ft, > SMR > 1.

Proof: For statum t of the covariate letXi •=» expected true number of unexposed controls,T( = expected exposure odds among controls (T, 'A Tj for some i, j)S = expected case-control ratio among the unexposed (S is constant across strata since the covariate is not a

risk factor).Then TtX( = expected number of exposed controls,

SXt " expected number of unexposed cases, andRSTiXj = expected number of exposed cases.

Also, the apparent numbers expected after misclassification will beAt = SXAQRTi + (1 — P)) = apparent number of exposed cases,Bt = SXAP + (1 — Q)RTt) •• apparent number of unexposed cases,Cj = XAQTj + (1 - P)) = apparent number of exposed controls, andDi = XAP + (1 — Q)Ti) •= apparent number of unexposed controls.

We will prove the theorem only for the case R > 1, T\ < To, as proofs for the other three cases follow bysymmetrical arguments.

For the binary case (i = 0 or 1 only), proof proceeds by the following lemmas:

Lemma 1. If R > 1 and 7\ < To, then BiD0 < BoDx.

Proof: By direct algebra, B^Do - BoD, - P(l - Q)(l - R)S(T0 -

1 - R is the only negative term in the right hand product, hence both sides of the equation are negative.

Lemma 2. If T, < To and P + Q > 1, then CtD0 < CoDi.

Proof: By direct algebra, CJ)l - C,D0 = (P + Q - 1)(TO - T,)X,.Xo.All the terms in the right hand product are positive, hence both sides of the equation are positive.

Lemma 3. If R > 1, 7\ < To, and C,D0 < CoDi, then SMR < fl,.

Proof: By Lemma 1 B,D0 - B<lDl < 0.Hence

506 GREENLAND AND ROBINS

C1D0(BlDB - BoD,) > CoD1(B1D0 -

yielding

then

BjdDo7 + BoCoD,1 > B,CoDiDc, +

Adding (B1C1 + Bt/Co)DiDo to both sides of the last inequality and factoring, we obtain

(fl,C,A> + BcCoDtHDt + Do) > (B, + flo)(C, + Co)Z),A,,

then

B.d/D, + BcCo/Do > (Bi + Bo)(C, + C)/^ + A,).

Dividing both sides of the last inequality into Ai + Ac, yields

SMRB<A/A>) (Bi + Bo)(C, + Co)

It is well known (e.g., see references 12, 13, and 18) that (within strata) nondifferential misclassificationproduces bias towards the null, hence ft > SMR > 1; unrelatedness of the covariate to classification impliesthat the misclassification is also nondifferential in the crude table and hence ft > fle. The theorem now followsfor binary covariates from Lemmas 1-3. Extension to the case of a covariate with K levels follows bymathematical induction: Suppose the theorem holds for K — 1 levels. Let SMR and ft^ be the expected internallystandardized and crude odds ratios obtained from all K covariate strata, SMR* and ft«* the correspondingexpected values obtained from the first K - 1 strata only, and let SMR. be the standardized odds ratio obtainedby collapsing the first K — 1 levels of the covariate before adjustment (Le., coding the covariate as "level K ornot-K"). Finally, let A*, B*, C*, and D* be the sum of the corresponding cells in the first K - 1 strata, and

W* = ]

Since SMR* = A'/W* < A*D*/B*C = ft/, we have B*C*/D* < W*, hence

SMR - WAIBZDK < *-cv£ t - '" = SMR"The binary case yields ftc > SMR,., hence i t > SMR. As before, we have R> R* and SMR > 1 as well, provingthe theorem.

Using arguments symmetrical to those given above, the theorem extends to the case in which the unexposedserve as the source of standardization weights (i.e., the "externally" standardized odds ratio), as well as anyaverage of the exposed and unexposed weightings (such as weighting based on the combined distribution). Thetheorem also extends to cohort studies by letting ft be the risk ratio, S the incidence in the unexposed, SMRthe usual cohort standardized morbidity ratio, and X, T, C, and D refer to quantities in the total cohort (ratherthan the controls). Finally, the theorem extends to case-control studies of populations with nondifferentialmisclassification of disease by letting Q and P refer to the disease sensitivity and specificity, and mumming thatthe covariate is unassociated with exposure (instead of disease) and that no refinement of diagnosis is made forthe study. We note, however, that the assumption of a constant odds ratio (in case-control studies) or risk ratio(in cohort studies) is necessary for the above results: examples show that under heterogeneity the misclassifi-cation bias in the crude ratio can sometimes exceed that in the standardized ratio. Such an example can beconstructed by modifying example 1 (tables 1 and 2) so that the true number of cases at F •=• C •» 1 ia 1.