Journal of Personality and Social Psychology1980, Vol. 39, No.6, 1037-1049

Perseverance of Social Theories: The Role of Explanationin the Persistence of Discredited Information

Craig A. Anderson, Mark R. Lepper, and Lee RossStanford University

The perseverance of social theories was examined in two experiments within adebriefing paradigm. Subjects were initially given two case studies suggestive ofeither a positive or a negative relationship between risk taking and success as afirefighter. Some subjects were asked to provide a written explanation of therelationship; others were not. In addition, experimental subjects were thoroughlydebriefed concerning the fictitious nature of the initial case studies. Subsequentassessments of subjects' personal beliefs about the relationship indicated thateven when initially based on weak data, social theories can survive the totaldiscrediting of that initial evidential base. Both correlational and experimentalresults suggested that such unwarranted theory perseverance may be mediated,in part, by the cognitive process of formulating causal scenarios or explanations.Normative issues and the cognitive processes underlying perseverance were ex-amined in detail, and possible techniques for overcoming unwarranted theoryperseverance were discussed.

All of us have tried to change a friend'sview about some social, political or scientificissue-from the efficacy of capital punishmentas a deterrent to crime to the validity of theIQ test-only to experience frustrating fail-ure. We offer seemingly compelling evidenceor thoroughly rebut opposing arguments butproduce little if any change in our friend'sbeliefs. Indeed, we suspect that we ourselvesfrequently may be guilty of similar intransi-gence when our views come under attack.From such everyday observations, two obviousquestions arise that form the focus of thepresent article: Are we, in fact, prone to per-sist in our beliefs and theories about theworld to a degree that is normatively inde-fensible, and if so, why?

This research was supported in part by ResearchGrants MH-26736 from the National Institute ofMental Health and BNS-78-01211 from the NationalScience Foundation to the second and third authors,and by a National Science Foundation Fellowship tothe first author. The authors wish to express theirthanks to Mark Zanna for his insightful commentson an earlier draft of this article and to DanBoeriu for his assistance in conducting Experiment 2.

Requests for reprints should be sent to CraigAnderson, who is now at the Department of Psy-chology, Rice University, Houston, Texas 77001.

The first, "normativeness," question inevi-tably proves to be a complex and subtle one,and we shall postpone much of our discussionof this question until we have presented de-tails about the present procedures and results.For now let us simply note that any consider-ation of the proposition that our beliefs areless responsive to empirical or logical attacksthan they "ought to be" requires that one beable to specify how much change in our beliefswould be warranted by any particular chal-lenge to those beliefs. Everyday observations,however, rarely permit such specification.Generally, all one can say with certainty isthat some change is warranted whenever theempirical or logical attacks seem to havemerit.

Nevertheless one case does arise in whichnormative standards seem less flexible. Werefer to circumstances in which all of the evi-dence that initially gave rise to a particulartheory is thoroughly and completely dis-credited. When all of the evidence on which Ihave based a belief, or based a change in be-lief, is shown to my satisfaction to be totallywithout evidential value-if, for example, allof it is shown to be fictitious-then most

Copyright 1980 by the American Psychological Association, Inc. 0022-3514/80/3906-1037$00.75

1037

1038 C. ANDERSON, M. LEPPER, AND L. ROSS

arbiters of normativeness would agree thatmy belief ought to revert to its original state.

To date, there is no experimental researchconcerning the perseverance of theories in theface of total evidential discrediting. Some per-tinent evidence exists, however, for one classof less abstract beliefs. It appears that spe-cific personal impressions in a given domainconcerning one's own abilities or those of apeer may survive even the complete invalida-tion of the evidence on which the impressionsinitially were based. Ross, Lepper, and Hub-bard (1975), for example, provided subjectswith false feedback indicating their apparentsuccess or failure at discriminating authenticsuicide notes from inauthentic ones, a taskpurported to assess their social sensitivity andempathetic ability. For half of the subjectsthe probative value of this feedback was sub-sequently completely negated by a thorough"debriefing" procedure. Although subjectsunderstood and accepted this "debriefing,"their predictions of future task success andratings of their own abilities continued to beheavily influenced by the discredited priorsuccess or failure feedback. Similar perse-verance effects were also apparent in the socialimpressions and predictions made by ob-servers who had witnessed the subjects' origi-nal outcomes and subsequent debriefings.Other experiments, carried out in more ap-plied contexts and with more naturalisticdiscrediting procedures, have shown that er-roneous first impressions about other abilitiessuch as "personal persuasiveness" (Jennings,Lepper, & Ross, Note 1) and "logical reason-ing" (Lepper, Ross, & Lau, Note 2) can like-wise survive the removal of their initial evi-dential basis.

A first major objective of the present ex-periments on theory perseverance, therefore,was to extend these previous findings regard-ing the unwarranted perseverance of initialbeliefs. On the one hand, we sought to showthat the perseverance phenomenon would ap-ply beyond the limited domain of highlyspecific personal and social impressions. Onthe other, we sought to demonstrate that per-severance effects may occur even when sub-jects' theories are initially based on minimal,~nd indeed logically inadequate, evidence-

when their beliefs are of exactly the tenta-tive, hastily-formed, and ill-founded varietymost likely to face subsequent logical or evi-dential discrediting in everyday experience.By focusing on tentative social theories, thestudies to be reported attempted to examinethe perseverance of beliefs that may occureven in the absence of strong emotional orbehavioral commitments, or logically com-pelling prior evidence.

At the same time, we also sought to addressa second major question, concerning themechanisms that may underlie theory per-severance, through a direct examination ofone cognitive process hypothesized to fosterbelief perseverance. This process involves theformulation of relevant causal scripts or ex-planations, and derives from people's pro-pensity to seek or construct explanations toaccount for salient events or relationshipsamong events that one has noted (d. Kelley,1967, 1973). Such causal accounts providethe perceiver with an important and efficientmeans of organizing and understanding thesocial world. Yet, because such accounts maybecome independent of the data that originallygave rise to them, they may contribute to theunwarranted persistence of initial impressionsand theories as well. Once a causal accounthas been generated, it will continue to implythe likelihood of the "explained" state of af-fairs even after the original basis for believingin that state of affairs has been eliminated(Ross & Anderson, in press; Ross & Lepper,in press). For example, the scientist who hasexplained why early humans might have in-habitated a particular region will continue tobelieve such inhabitation is likely even afterthe fossil evidence that originally promptedthe explanation has been thoroughly dis-credited. Consistent with this analysis, Ross,Lepper, Strack, & Steinmetz (1977) haveshown that providing an explanation for somepossible outcome in an individual's life in-creases the subjective likelihood of that out-come. Fischhoff's provocative investigations ofhindsight phenomena (e.g., Fischhoff, 1975)similarly suggest the power of causal explana-tions to influence expressions of likelihood oreven inevitability. The role of such explana-tion processes in the perseverance of social

PERSEVERANCE OF SOCIAL THEORIES

theories, however, has not received previousstudy. .

The two studies that follow, therefore,examine the operation of this explanationmechanism in the perseverance of theoriesbased on inadequate initial evidence. In bothexperiments subjects were asked to explainan empirical relationship-that existing be-tween success in the occupation of firefighterand preference for risk as measured by apaper and pencil test-just before learningthat the "evidence" that initially had ledthem to believe in that relationship was en-tirely fictitious. In Experiment 1, the explana-tion task was introduced for all subjects; itwas designed primarily to enhance the likeli-hood of belief perseverance, but it also per-mitted us to correlate the quality of an ex-planation with its impact on the subject'spostdiscrediting beliefs. In Experiment 2 in-clusion versus exclusion of the explanationtask was deliberately manipulated, allowingus to contrast directly the magnitude oftheory perseverance in the presence and ab-sence of the interpolated explanation task.Our interest in these studies thus focused ontwo main questions: First, would subjectscontinue to hold a given theory about an em-pirical relationship between variables after themeager evidential basis for that theory hadbeen invalidated? Second, would the processof providing an explanation for a given rela-tionship increase subjects' tendency to per-severe in their theories following this dis-crediting procedure?

Experiment 1

In our initial experiment, subjects werefirst led to believe that either a positive ornegative relationship existed between atrainee's preference for risky versus conserva-tive choices and his subsequent success as afirefighter, and were asked to provide a writ-ten explanation of this relationship. Subjectsin "debriefing" conditions were then explicitlyinformed that the initial information they hadbeen asked to consider was bogus and of ab-solutely no probative value. This debriefingwas omitted for a group of "no debriefing"subjects. All subjects then completed several

1039

dependent measures assessing their beliefsconcerning the true relationship between thesetwo variables and the predictive power of therelationship. A baseline control group re-ceived no information about the relationshipbetween the two variables but completed thevarious dependent measures. The final designwas thus a 2 X 2 factorial (Positive vs.Negative Relationship X Debriefing vs. NoDebriefing), with an added baseline controlgroup.

MethodSub jects

Seventy Stanford undergraduates, participating ingroups of two to eight, took part in the experiment,for which they received course credit. Since sub-jects in the experimental groups were to receive in-structions that differed slightly from those in thebaseline control group, these latter subjects partici-pated in separate sessions. Within the experimentalconditions, subject assignment was randomized inblocks of 12, and the experimenter remained blindto subjects' conditions.

Procedure

Experimental subjects were told that the experi-ment was concerned with how well people are ableto discover and explain relationships between per-sonal characteristics of people and their behavioraloutcomes. They were informed that they would beasked to examine some data and to see if they couldd'scover and subsequently explain underlying rela-tionships between general traits and specific be-haviors, Control subjects were told simply that theywould be asked to make predictions concerning theabilities of persons as a function of their perform-ance on a test of risk preference. After answeringany questions about these general instructions, theexperimenter gave subjects booklets containing theexperimental materials.

ManiPulation of initial theories. Booklets for sub-jects in the experimental conditions first stated thatthe subject's task was to examine the relationshipbetween eventual success or failure as a firefighterand prior performance on a "Risky-ConservativeChoice Test" (RCC test). Next, nondiagnostic back-ground information (age, marital status, hobbies,etc.) for one successful and one unsuccessful fire-fighter was presented, along with each firefighter'sresponses to the five "most representative" risky-conservative choice problems. Subjects were in-structed to examine this information about riskinessand ability, to attempt to discover the underlyingrelationship, and to provide a written explanationof any relationship they uncovered.

1040 C. ANDERSON, M. LEPPER, AND L. ROSS

In all conditions the RCC test items were similarto items used previously in research on group-induced shifts to risk taking. Each item presenteda dilemma and two possible behavioral alternatives,one risky and one conservative. Each response was ashort paragraph, purportedly written by the fire-fighter, that gave his choice of action and explana-tion of the choice. For half the subjects, the pur-ported responses were arranged to demonstrate apositive relationship between risky choices and latersuccess as a firefighter; for the remaining subjects,these responses were arranged to demonstrate anegative relationship between risky choices and suc-cess as a firefighter.

To ascertain that subjects had indeed "discovered"different relationships in these two conditions, amanipulation check was included immediately beforethe explanation task. The results from this measure-a lOl-point scale anchored at "Highly Positive Re-lationship" (50), "No Relationship" (0), and "HighlyNegative Relationship" (-50)-indicated that sub-jects in the positive relationship qmditions did "dis-cover" a positive relationship, M = 33.87, t(54) =9.99, P < 00001, whereas subjects in negative rela-tionship conditions "discovered" a negative rela-tionship, M = 7,7,57, t(54) = 1,1,1, P < 000001After completing these measures, all subjects wereasked to provide a one-page, written explanation ofthe relationship they had uncovered in the two casestudies.

Debriefing manipulations. Within the two rela-tionship conditions, two thirds of the experimentalsubjects were assigned, at random, to the debriefingconditions.1 These subjects received a detailed, writ-ten debriefing following the explanation task inform-ing them that they had been randomly assigned thetask of discovering and explaining either a positiveor a negative relationship between risk preferenceand success as a firefighter. To insure that subjectsdid not still perceive the case data they had re-ceived to be representative of a true relationship,subjects were also explicitly informed that the ex-perimenters had provided fictitious information con-sistent with a positive relationship or a negativerelationship to subjects in different conditions, andthat the experimenters did not know the nature orstrength of the "true" relationship.

The last section of the debriefing materials ex-plained to subjects that the prediction and estima-tion tasks to follow were for "control purposes," tosee if their personal theories about the relationshipin question had influenced their discovery of a rela-tionship or the quality of their explanations. Sub-jects were urged to make all their judgments basedon their personal beliefs and not the fictitious infor-mation initially presented. During final postexperi-mental debriefing sessions, all subjects indicated anawareness and understanding of these critical in-structions.

Subjects in the no-debriefing conditions receivedno such information. After completing their explana-tions, these subjects proceeded directly to the de-pendent measures. Control subjects received book-

lets informing them that their task was to examinethe information within, and they were also asked tomake their predictions and estimates based on theirpersonal beliefs. These subjects were given no in-formation about the relative success of the twocase study firefighters, nor were they asked to ex-plain any relationship between risk preference andtask success. In all other respects, all subjects re-ceived identical materials and completed identicalmeasures.

Dependent measures. Several dependent measureswere employed, each designed to assess subjects' be-liefs concerning the true relationship between apreference for risky choices and ability as a fire-fighter. To minimize the relevance of social evalu-ation concerns, these measures were collected underconditions of anonymity.

The first of these measures asked subjects to judgedirectly the "criterion validity" of the risk preferencescale as an index of fire fighting ability. Subjectswere asked to estimate the average percentage ofrisky choices for two groups of firefighters-thosewho had subsequently become highly successful andthose who had been failures at the job. The per-ceived criterion validity of the RCC test was as-sessed by subtracting the expected percentage ofrisky responses among failure firefighters from theexpected percentage of such choices among success-ful firefighters, yielding a difference score that couldrange from 100 (a maximally strong positive rela-tionship) to 1010 (a maximally strong negativerelationship) .

A second set of measures dealt with subjects'willingness to generalize, on the basis of their beliefsabout the riskiness-success relationship, in makingpredictions about new cases and new items. For theformer measure, subjects were presented with infor-mation on four new trainees, including both non-diagnostic background evidence (e.g., father's occu-pation, marital status, etc.) and the individual'sresponse to one RCC Test item. Subjects then pre-dicted each trainee's subsequent success, allowing a

1 Two types of debriefing were used, both of whichfully invalidated the "evidence" initially presented.In "ability debriefing" groups, subjects were in-formed that the relative abilities of the two samplefirefighters had been manufactured but that the re-mainder of the information about them (Le., theirriskiness responses) had been authentic. In the "traitdebriefing" groups, the riskiness information wasdiscredited, but the ability information was allowedto stand. This variation was introduced to seewhether subjects would be more responsive to dis-counting of one type of information than another.Preliminary analyses yielded no consistent effects ofthe two variants of the debriefing. Hence, the datawere collapsed across this dimension in all tables,and in all further analyses equal contrast weightswere assigned to the two debriefing conditions withinthe positive or negative relationship manipulations(see Winer, 1971).

Negative relationship

No debrief Debrief Control

-14.2 -1.3 25.5-2.0 -1.3 .2~10.9 -5.5 19.410 20 10

PERSEVERANCE OF SOCIAL THEORIES 1041

Table 1Mean Postexperimental Beliefs Concerning RelationshiP Between Risk Preferenceand Firefighter Success: Experiment 1

Dependent measure No debrief

Positive relationship

Debrief----

Perceived criterion validity'Generalization to new casesbGeneralization to new itemsc

n

51.81.4

41.810

36.01.1

31.720

----Note. Positive scores indicate belief in a positive relationship; negative scores indicate belief in a negativerelationship..Predicted percentage of risky responses on the risky-conservative choice test for superior minus unsuccess-ful firefighters. Range of possible scores is 100 to 0000.b (Number of success-risky + number of failure-conservative) - (number of success-conservative + num-ber of failure-risky) predictions to four new cases. Range of possible scores is 4 to .4.c Predicted percentage of risky responses on five new items for superior minus unsuccessful firefighters.Range of possible scores is 100 to 0000.

test of the extent to which their predictions con-formed to those that would follow from beliefs in apositive or a negative relationship between RCCscores and occupational success. For the latter mea-sure, subjects were presented with five novel hypo-thetical-choice items in the same general format asthose in the RCC test, and were asked to indicatethe percentage of risky choices that superior andinferior firefighters would make on these items. Adifference score served as an index of the subjects'willingness to generalize to new test items on thebasis of their correlational theory. At the completionof the experiment, subjects were probed for sus-picion and given a thorough explanation of theprocedures and purposes of the study and of theprocesses that may mediate the unwarranted per-severance of initial beliefs.

Results and Discussion

The results for each of these three measuresare presented by condition in Table 1. As onemight expect, the three measures proved tobe highly intercorrelated (average r = 7373.

Thus, the data on each were transformedinto Z scores and summed to provide a com-posite measure of subjects' beliefs concerningthe true relationship between risk preferencesand subsequent success as a firefighter. Thedata from these composite scores are pre-sented in Figure 1, and it is on these datathat our primary analyses were performed. 2

We should first note, perhaps, that al-though the "data" to which subjects had beeninitially exposed were objectively quite weak(consisting of only two cases) and in a

domain of little personal relevance, this initialostensible evidence clearly exerted a strongeffect on subjects' theories about the truerelationship between the two variables. Thus,in the no-debriefing conditions, subjects ex-posed to a positive relationship saw riskyresponses as highly diagnostic of later suc-cess, whereas subjects exposed to an apparentnegative relationship believed the opposite tobe true, F(l, 63) = 20.21, P < 00001.

Given these clear effects of initial informa-tion on subjects' beliefs prior to debriefing,it is possible to examine the perseverance ofthese beliefs in the debriefing conditions,after subjects learned that the two casestudies were fictitious. As is evident in Figure1, the total discrediting of the evidence onwhich subjects' initial theories had beenbased had only a minimal impact on subjects'beliefs concerning the relationship betweenrisk preference and firefighting ability. Withinthe debriefing conditions, subjects initiallyexposed to data indicative of a positive rela-tionship continued to believe that a positiverelationship existed, whereas subjects in thenegative relationship condition continued to

2 Separate analyses parallel to those to be reported

below were also performed for each of the threecomponent measures. In all cases, effects that provedstatistically significant in the combined analyses wereindividually significant (p < 5)5) for each of the

three component measures as well.

1042 C. ANDERSON, M. LEPPER, AND L. ROSS

+2

~POSITIVERELATIONSHIPCONDITIONS

DNEGATIVERELATIONSHIPCONDITIONS

CLI +1<f)zQ

~~ 00w~?;tn -1w

-2

NO DEBRIEFING DEBRIEFING CONTROL

TREATMENT CONDITIONS

Figure 1. Mean composite indices (Z scores summedacross the three measures) of subjects' personalestimates of the true relationship between risk prefer-ence and firefighter success, Experiment 1. (Positivescores indicate belief in a positive relationship;negative scores indicate belief in a negative relation-ship.)

believe in a negative relationship, F ( 1, 63) =17.43, P < 00001. In fact, the slight decreasein the strength of subjects' beliefs followingdebriefing, as assessed by the Relationship XDebriefing interaction, was not statisticallysignificant, F( 1, 63) = 1.59.

These effects, moreover, were roughly sym-metrical with respect to the responses of con-trol subjects not initially exposed to the twocase studies, who tended to believe that therewould be a slight positive relationship be-tween a preference for risky choices and latersuccess as a firefighter. Consideration of thedebriefed groups and the control group in aone-way analysis of variance yielded strongevidence of a monotonic relationship betweeninitial information and' subsequent beliefs,monotonic contrast F(I, 45) = 16.13, P <00005, with a nonsignificant residual, F(3,45) = 1.24.

In sum, the results strongly support thehypothesis that even after the initial evi-dential basis for their beliefs has been totallyrefuted, people fail to make appropriate re-visions in those beliefs. That subjects' theoriessurvived virtually intact is particularly im-

pressive when one contrasts the minimalnature of the evidential base from whichsubjects' initial beliefs were derived (Le., two"data points"), with the decisiveness of thediscrediting to which that evidence was sub-jected. In everyday experience our intuitivetheories and beliefs are sometimes based onjust such inconclusive data, but challenges tosuch beliefs and the formative data for thosebeliefs are rarely as decisive as the discredit-ing procedures employed in this study.

If our speculations about underlying mech-anisms are correct, however, the design ofExperiment 1 also included one feature thatis only occasionally present in everydayexperience, but that should have served to aug-ment any perseverance effects-the require-ment that subjects provide an explicit ex-planation for the relationship they had ob-served. While Experiment 1 contains no directevidence on this issue, some indirect supportfor this hypothesized perseverance-enhancingeffect of explanation is provided by an in-ternal analysis of the relationship between thenature of subjects' explanations and the per-sistence of their initial theories followingdebriefing.

Although an unintended source of variancein our procedure, the explanations subjectsprovided proved to be of two distinct types.Some subjects responded to the request asintended, offering some general causal accountthat explained the specific case studies theyhad read. These accounts typically focused onthe risks inherent in fighting fires and theimportance, depending on condition, of eithera willingness to take necessary risks or theneed to avoid foolhardy and impulsive actionas a determinant of successful performance.Other subjects apparently construed the taskdifferently. These subjects simply "explained"how the specific information contained in thetwo particular case studies they had readillustrated either a positive or a negative re-lationship-they basically restated the factthat the more successful candidate had se-lected considerably more risky, or more con-servative, alternatives than his less successfulcounterpart.

Theoretically, the effects of these two sortsof explanations on belief perseverance should

PERSEVERANCE OF SOCIAL THEORIES

differ, since only subjects in the former casehave generated principles that should con-tinue, even after debriefing; to imply theexistence of the relationship they had initiallyobserved. Only in this first case should ex-planations enhance theory perseverance. Con-sistent with this analysis, the data revealed ahighly significant point-biserial correlation be-tween the presence or absence of general ex-planatory principles in subjects' explanationsand the degree of postdebriefing belief per-severance, r = 4,4, P < 00005.

Experiment 2

Experiment 1 demonstrated that a theoryconcerning the relationship between two vari-ables-generated through exposure to a mini-mal data set-can survive even a completerefutation of the formative evidence on whichthe theory was initially based. Questions re-main, however, concerning the role of theexplanation processes in mediating these per-severance effects-an issue to which Experi-ment 2 was directed.

Specifically, Experiment 2 addressed twoprimary questions: Whether explicit explana-tion is a necessary precondition for the post-discrediting perseverance of a theory or, ifnot, whether it nevertheless increases themagnitude of such perseverance. To addressthese issues, Experiment 2 compared six con-ditions. As in Experiment 1, all subjects werefirst presented with information on illustra-tive cases involving one highly successful andone clearly unsuccessful firefighter and wereasked to discover the relationship betweenrisk preference and firefighting ability-eitherpositive or negative-contained in these casedata. Within these conditions, one third ofthe subjects were next asked to write an ex-planation of the discovered relationships andwere then debriefed concerning the fictitiousnature of the case study materials, as in Ex-periment 1. No mention of explanation wasmade in the remaining four conditions. Inthese no explanation conditions, half of thesubjects were debriefed concerning the fic-titious nature of the experimental materials;the remainder were not debriefed. The effectsof exposure to initial evidence illustratingeither a positive or a negative relationship

1043

were thus examined under three variations ofdebriefing and explanation: debriefing-ex-planation, debriefing-no explanation, and nodebriefing-no explanation. Finally, as before,all subjects completed a set of dependent~easures assessing their beliefs concerningthe nature of the actual relationship betweenthe two critical variables.

Method

Subjects in Experiment 2 were 62 Stanford Uni-versity undergraduates, who received credit towardan introductory psychology class requirement or$2.00 for their participation in the study. Datafrom two subjects who failed to complete the testmaterials were not used. Procedures, booklets, andinstructions were basically identical to those ofExperiment 1, with only those changes necessary toaccommodate the new design of this second study.Thus, all subjects were initially presented with thesame case study materials used in Experiment 1,suggesting either a positive relationship between riskpreference and subsequent success or a negativerelationship between these variables. Orthogonally,subjects in two sets of debriefing conditions werefully debriefed concerning the fictitious nature ofthese putative initial data.3 Prior to debriefing,however, half of these subjects were asked to pro-vide an explicit explanation of the relationship theyhad uncovered in the case studies; half were notgiven this explanation task. For purposes of com-parison, subjects in the no-debriefing conditions wereexposed to the initial data but were neither de-briefed concerning its fictitious character nor askedto explain the relationship they had uncovered.Following these procedures, as before, three mea-sures of subjects' personal beliefs concerning thetrue relationship between these variables-the per-ceived criterion validity of the RCC Test and gen-eralization to new case studies and new test items-were anonymously assessed. Finally, all subjects wereprobed for suspicion and given a complete explana-tion of the procedures and purposes of the studyand the processes that may mediate the unwarrantedperseverance of initial beliefs.

Results

The results from these three measures ofsubjects' subsequent beliefs concerning the

3 To provide an even more complete discrediting ofthe data on which subjects' initial beliefs rested,subjects in Experiment 2 were informed that thetwo case studies were entirely fictitious, that is,that both the ability ratings and the risk preferenceinformation had been manufactured by the experi-menters and had been randomly assigned to them.

Positive relationship Negative relationship

No debrief- Debrief-' Debrief- No debrief-- Debrief- Debrief-Dependent measure no explain explain no explain no explain explain no explain

Perceived criterionvalidity' 54.0 39.0 39.5 -57.4 -35.3 -14.0

Generalizationto new casesb 2.2 1.0 0.2 -3.0 -2.8 -.6

Generalizationto new itemsc 42.1 37.1 26.1 -38.5 -30.5 -9.9n 10 10 10 10 10 10

1044 C. ANDERSON, M. LEPPER, AND L. ROSS

Table 2Mean Postexperimental Beliefs Concerning Relationship Between Risk Preferenceand Firefighter Success: Experiment 2

Note. Positive scores indicate belief in a positive relationship; negative scores indicate belief in a negativerelationship..Subjects' predicted percentage of risky responses on the risky-conservative choice test for superior minusunsuccessful firefighters. Range of possible scores is 100 to 0000.b (Number of success-risky + number of failure-conservative) - (number of success-conservative + num-ber of failure-risky) predictions to four new cases. Range of possible scores is 4 to .4.c Subjects' predicted percentage of risky responses on fitte new items for superior minus unsucc('ssful fire-fighters. Range of possible scores is 100 to 0000.

relationship between risk preference and sub-sequent job success are presented in Table 2.As in Experiment 1, these measures proved tobe highly intercorrelated (average r = 4)4).

Hence composite Z scores summing acrossthree measures were again calculated, andanalyses were conducted on these compositescores, illustrated in Figure 2.4

From these data, it is clear that exposureto the two initial case studies again exerted apowerful effect on subjects' later beliefs; no-debriefing subjects exposed to a positive rela-tionship saw risky responses as indicative offuture success, whereas those exposed to anegative relationship believed the opposite tobe true, F(I, 54) = 125.76, P < 00001. Theseinitial differences in beliefs between the posi-tive and negative relationship conditions per-sisted even after subjects had been thoroughlydebriefed in both the debriefing-explanation,F(I, 54) = 69.74, P < 00001, and the debrief-ing-no-explanation, F(I, 54) = 19.24, P <00101, conditions. At the same time, it is alsoapparent that subjects' beliefs were not whollyunaffected by the debriefing manipulation.Within the no-explanation conditions, de-briefed subjects endorsed less extreme theoriesthan did nondebriefed subjects, as indicated

by a significant Relationship X Debriefinginteraction within these four cells, F (1, 54) =23.31, P < 00001.

To test our further hypothesis that theoryperseverance would be enhanced when sub-jects had been specifically induced to providean explanation of the theory required a con-sideration of the interaction between the ex-planation and relationship manipulationswithin the four debriefing conditions of thisstudy. The relevant interaction term, as pre-dicted, showed that the process of explainingthe relationship observed in the initial casestudies significantly enhanced the perseverance

;. 4 As in Experiment 1, separate analyses parallel tothose performed on the composite belief measure

""ere again performed for each of the three com-ponent measures separately. All effects to be reportedbelow proved individually significant (p < 5)5) for

each of the three measures, with two exceptions:For the perceived criterion validity measure, thE;J:;xplanation X Relationship interaction term was not

.,.,

individually significant, F(1, 54) = 1.71, and for thegeneralization to new cases measure, the post-debrief-ing perseverance effect within the no-explanationconditions was not significant (F < 1). As is evidentfrom Table 2, however, even in these cases the meansfall in the predicted direction.

PERSEVERANCE OF SOCIAL THEORIES

+6

~POSITIVERELATIONSHIPCONDITIONS

DNEGATIVERELATIONSHIPCONDITIONS

+4[LI<f)

z +20

~--'Ii! 0

0w~ -2:;;f-<f)w

-4

0

L--

- 6 f- L--J 'NO DEBRIEFING DEBRIEFING DEBRIEFINGNO EXPLANATION EXPLANATION NO EXPLANATION

TREATMENT CONDITIONS

Figure 2. Mean composite indices (Z scores sumfhedacross the three measures) of subjects' personalestimates of the true relationship between risk pr~er-ence and firefighter success, Experiment 2. (Positivescores indicate belief in a positive relationship; nega-tive scores indicate belief in a negative relationship.)

of subjects' beliefs in the relationship theyhad discovered, F(l, 54) = 7.86, P < 1.1.5

General Discussion

The results of these two experiments pro-vide support for three general conclusions.First, they offer further evidence for the basichypothesis that people often cling to theirbeliefs to a considerably greater extent thanis logically or normatively warranted. Theexperiments thus extend previous research onthe perseverance of specific self-assessmentsand interpersonal judgments to the m0regeneral domain of theories concerning r~la-tionships among social variables. Second, th~sestudies also extend prior research by suggtfst-ing that initial beliefs may persevere in theface of a subsequent invalidation of the tWi-dence on which they are based, even wBen

~.~this, ini~ial evjde~ce is i~self as ,:eak and in-

.. conc:luslve as a sIngle paIr of dubIOusly rep'i'e-

sentative cases. Finally, the current resultsprovide support for the hypothesis that beliefperseverance effects may be mediated, in part,by the generation of causal explanations orscenarios that continue to imply the correct-

1045

ness of one's initial beliefs even in the laterabsence of any directly relevant evidence.

Before considering the implications of thesefindings in greater detail, however, it is im-pOl'taut to consider two potential alternativeexplanations of these results. A first possibil-ity is that subjects in the debriefing condi-tions simply failed to understand or believethe discrediting information provided duringdebriefing. Some presumptive evidence againstthis argument, of course, is provided by thefact that the debriefing procedure did seemto affect subjects' subsequent beliefs. De-briefed subjects consistently reported lessstrong beliefs than subjects who were notdebriefed, an effect that proved individuallysignificant in the second experiment. Perhapsmore persuasive, however, were the results ofpostexperimental discussions with subjects inwhich they indicated that they were neitherconfused about nor suspicious of the debrief-ing manipulation: In all cases, during thisfinal debriefing period, subjects seemed ableto describe accurately the content of the dis-crediting procedure, and in no case did sub-jects voice any suspicion that this informationmay have been untrue. Instead, they simplyfelt that the relationship they had examined-whether positive or negative-appeared to bethe correct one and that the discrediting ofthe evidential value of the initial cases waslargely irrelevant to their personal beliefsconcerning the "true" relationship existingbetween these variables. Interestingly, intheir attempts to aid us as experimenters,several subjects expressed concern over theimplausibility of the relationship given to

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5 The difference between the designs of Experi-ments 1 and 2 meant that only half as many subjectsin the latter experiment were called on to provideexplanations prior to debriefing. Nevertheless, in-ternal analysis examining the relationship betweenthe presence of some generalized explanatory scenarioor principle in subjects' explanations and the per-severance of subjects' beliefs following debriefingwas again performed. Although in the same directionas in the first experiment, this correlation was notsignificant, r = 121 (nor was it significantly differentfrom the comparable correlation obtained in Experi-ment 1). The weighted average of these correlations(McNemar, 1962), we should note, remains highlysignificant, rav = 44, P < OOOOS.

1046 C. ANDERSON, M. LEPPER, AND L. ROSS

subjects in the opposite relationship condi-tion. As one subject in a positive relationshipcondition commented, "I don't think yourexperiment will work, since it will be im-possible to convince anybody that the truerelationship is negative." In short, we areled to discount any alternative account of thepresent results that rests on an alleged failureof subjects to comprehend or accept the dis-crediting information provided.

A second alternative explanation involvesthe possibility that the check on our manipu-lation of subjects' initial theories in thesestudies, because it required subjects to stateexplicitly their beliefs prior to debriefing,may have introduced a potential artifactwhereby subjects subsequently reported be-liefs consistent with their prior statements,via classic dissonance or self-perception pro-cesses. This appears improbable for two rea-sons. First, subjects' responses to the manipu-lation check were obtained under preciselythe type of conditions-high justification,low choice, and little consequence-thatshould theoretically have minimized any ex-perience of dissonance or conviction that theirresponses reflected their enduring beliefs. Infact, subjects at this point were asked onlyto describe the relationship that they haddetected in the two case studies at hand, nottheir beliefs about the relationship that mightexist between the two variables in general.Second, available data suggest that the presenteffects do not depend on the presence of sucha manipulation check. If this proposed al-ternative were correct, a condition in whichsubjects were not asked to state their beliefsprior to debriefing should not show a perse-verance effect. In a previous study that madeuse of the same experimental materials andbasic procedures as the present experiments(Anderson & Ross, Note 3), however, signifi-cant perseverance effects, paralleling those re-ported here, were obtained in the absence ofsuch manipulation checks.

In light of the apparent clarity of our re-sults, then, let us consider further the impli-cations of belief perseverance effects. Weshould make clear that a tendency to per-severe in one's previous beliefs is not alwaysdetrimental, or even illogical. Indeed, in cases

where our existing theories have already re-ceived significant support from differentsources, it might be more irrational not toview subsequent challenges to those beliefs,or the evidence on which they were initiallybased, with an appropriately jaundiced eye(d. Lord, Ross, & Lepper, 1979; Nisbett &Ross, 1980; Ross & Lepper, in press). To bebuffeted about by every random piece of dis-confirming data or every challenge to the evi-dential basis for one's beliefs, whether in thecourse of scientific inquiry or in our dailylives, will frequently prove less adaptive thana tendency to persist in theories that haveproven effective over time. What is particu-larly striking in the present study, therefore,is the demonstration of perseverance biases ina situation where subjects' theories wereinitially grounded in the most minimal of datasets-only two case studies. That subjectswill persevere in beliefs with such weak em-pirical grounding in the face of a completerefutation of the formative evidence for thosebeliefs seems eloquent testimony to the per-vasiveness of our propensity to resist chang-ing our attitudes or beliefs.

Even under these relatively extreme cir-cumstances, however, it is not clear that everyparticular instance of belief perseveranceshould be viewed as unreasonable or counter-normative. For example, exposure to even ademonstrably inadequate data set might leadone to appreciate the role of potential causalmechanisms that might have produced such adata set. Or it might lead one to recall orrecognize additional evidence that is not sub-sequently undermined and that had hereto-fore been given insufficient weight in one'sformulation of beliefs. Under such circum-stances persistent changes in belief in thedirection suggested by ultimately discrediteddata may be quite appropriate. In any givencase, therefore, the rationality of suchchanges will depend on the status of the indi-vidual's own prior beliefs and of the evidenceand reasoning that originally underlay thosebeliefs.

These caveats about overly quick and facilecharges of "counternormativeness," however,should not obscure an essential feature of thepresent findings. Specifically, we demonstrated

PERSEVERANCE OF SOCIAL THEORIES

that different subjects-and, by inference, thesame subject, if placed in different experi-mental conditions-can be led, with equalease through exposure to one data set or theother, to adopt and persevere in beliefs thatare conceptually opposite to each other. Theactual relationship between the two variablesconsidered cannot be simultaneously bothmore positive and more negative than our sub-jects initially believed it to be. Our argument,then, is not that the mechanisms underlyingbelief perseverance are inherently irrational orinevitably dysfunctional. Rather, we are sug-gesting that these mechanisms, like manyother processes underlying human inference(d. Nisbett & Ross, 1980; Ross & Anderson,in press; Ross & Lepper, in press), may leadin certain contexts to a normatively unwar-ranted judgment, belief, and behavior.

Perhaps most importantly, the presentfindings provide some direct evidence con-cerning the processes postulated to underliebelief perseverance. Our research demon-strated that belief perseverance is enhancedwhen subjects are explicitly induced to ex-plain the evidence they have been shown.Clearly, it is a central postulate of currentattribution models that people often engagein informal causal analyses in attempting tomake sense of their social worlds (Heider,1958; Kelley, 1967, 1973). The likelihood ofsuch attribution processes presumably varieswith the novelty, complexity, and personalrelevance of the events or outcomes one is at-tempting to understand (as well as with thedirect instructional manipulations of the sortemployed in the present studies). Such ex-planations may differ dramatically in theirlogical and formal properties, and may rangefrom the postulation of a set of antecedentconditions necessary or sufficient to producea given effect or outcome to a more simpleimagination of some relatively concretescenario in which the event or outcome fol-lows some previous state or condition. In thepresent studies, for example, subjects madefrequent use of one or another of two basicscenarios to explain either a positive or anegative relationship between risk preferenceand firefighting ability. In the positive rela-tionship conditions, subjects' explanations

1047

often included some contrast between thesuccessful firefighter braving enormous per-sonal risks to save the occupants of a burningbuilding and his unsuccessful counterpart,playing it safe, who stands by helplessly aslives are lost. In the negative relationshipconditions, by contrast, subjects' explanationsoften made reference to an alternative scenarioin which the successful firefighter carefullyweights the relevant risks before taking ap-propriate and decisive action, while the un-successful trainee plunges headlong intodanger, risking both his own and others' livesby foolhardy actions.

That such explanatory scripts or moreformal and abstract explanations-whethergenerated spontaneously by subjects or pro-duced in response to direct experimental in-structions-should increase belief perseveranceseems an obvious consequence of two proper-ties of these explanatory accounts. First, suchexplanations are, by definition, selectivelyconstructed to fit the evidence or outcomeobserved. Second, once created, such explana-tions become largely autonomous of the initialdata that led to their postulation. Hence, theymay remain available and continue to implythe existence of particular relationships oroutcomes even if the data on which they wereinitially based subsequently prove to be com-pletely devoid of evidential value. Evidenceof a positive relationship between the presenceof some general explanatory principle or scriptin subjects' explanations and the magnitudeof subsequent belief perseverance effects,moreover, provides some direct evidence forsuch processes. Subjects who devoted equaltime and effort to the explanation task butwho focused solely on the specifics of the twosubsequently discredited case studies did notseem to show increased perseverance.

There is, of course, one further assumptionimplicit in the foregoing account of our find-ings-that subjects, having explained the ap-parent existence of a particular relationship,are not led by our debriefing procedure togenerate any corresponding counterexplana-tion to account for an opposite pattern ofdata that might have been observed (Ross &Lepper, in press; Slovic & Fischhoff, 1977).

1048 C. ANDERSON, M. LEPPER, AND L. ROSS

ReferencesSuch an assumption is consistent with theproposition that people are likely to engagein the cognitive effort required to generate anexplanation only when provided with somesalient or unexpected event or outcome(Fischhoff, 1977; Kanouse, 1971; Lepper,lanna, & Abelson, 1970). It suggests, inaddition, an interesting potential antidote forunwarranted belief perseverance in the face oflater challenges to the evidence on which ourbeliefs were based. Would such perseveranceeffects be eliminated or attenuated, for ex-ample, if subjects could be led, after debrief-ing, to consider explicitly the explanationsthat might be offered to support a contentionin opposition to their initial beliefs? Alterna-tively, could subjects be "innoculated" againstperseverance effects if they had been asked,at the outset of the study, to list all of thepossible reasons they could imagine that mighthave produced either a positive or a negativerelationship between the two variables beingstudied (cf. Slovic & Fischhoff, 1977)? Inview of the pervasive significance of oursocial theories in decision-making contexts(d. Abelson, 1976; Janis & Mann, 1977), andthe demonstrable adverse effects of unwar-ranted belief perseverance in applied andclinical contexts (Allport, 1954; Chapman &Chapman, 1969; Janis & Mann, 1977; Lep-per, Ross, & Lau, Note 2), the effectiveness ofsuch debiasing techniques clearly merits fur-ther investigation.

Reference Notes

1. Jennings, D. L., Lepper, M. R., & Ross, L. Per-sistence of impressions of personal persuasiveness:Perseverance of erroneous self-assessments outsidethe debriefing paradigm. Unpublished manuscript,Stanford University, 1980.

2. Lepper, M. R., Ross, L., & Lau, R. Persistence ofinaccurate and discredited personal impressions:A field demonstration of attributional persever-ance. Unpublished manuscript, Stanford Univer-sity, 1980.

3. Anderson, C. A., & Ross, L. The survival of the-ories in the absence of evidence. Paper presentedat the Meeting of the Western Psychological As-sociation, San Francisco, 1978.

Abelson, R P. Script processing in attitude forma-tion and decision-making. In J. S. Carroll & J. W.Payne (Eds.), Cognition and social behavior.HiJlsdale, N.J.: Erlbaum, 1976.

AlIport, G. W. The nature of prejudice. Reading,Mass.: Addison-Wesley, 1954.

Chapman, L. J., & Chapman, J. P. Illusory corre-lation as an obstacle to the use of valid psycho-diagnostic signs. Journal of Abnormal Psychology,1969, 74, 271-280.

Fischhoff, B. Hindsight =Fforesight: The effect ofoutcome knowledge on judgment under uncer-tainty. Journal of Experimental Psychology:Human Perception and Performance, 1975, 1, 288-299.

Fischhoff, B. Perceived informativeness of facts.Journal of Experimental Psychology: HumanPerception and Performance, 1977, 3, 349-358.

Heider, F. The psychology of interpersonal relations.New York: Wiley, 1958.

Janis,!. L., & Mann, L. Decision making: A psy-chological analysis of conflict, choice, and com-mitment. New York: Free Press, 1977.

Kanouse, D. E. Language, labeling, and attribution.In E. E. Jones, et al. (Eds.) , Attribution: Per-ceiving the causes of behavior. Morristown, N.J.:General Learning Press, 1971.

Kelley, H. H. Attribution theory in social psychol-ogy. In D. Levine (Ed.), Nebraska symposium onmotivation (Vol. 15). Lincoln: University ofNebraska Press, 1967.

Kelley, H. H. The processes of causal attribution.American Psychologist, 1973, 28, 107-128.

Lepper, M. R., lanna, M. P., & Abelson, R P.Cognitive irreversibility in a dissonance-reductionsituation. Journal of Personality and Social Psy-chology, 1970, 16, 191-198.

Lord, C., Ross, L., & Lepper, M. R Biased assimila-tion and attitude polarization: The effects of priortheories on subsequently considered evidence.Journal of Personality and Social Psychology,1979, 37, 2098-2109.

McNemar, Q. Psychological statistics. New York:Wiley, 1962.

Nisbett, R. E., & Ross, L. Human inference: Strate-gies and shortcomings of social judgment. Engle-wood Cliffs, N.J.: Prentice-Hall, 1980.

Ross, L., & Anderson, C. Shortcomings in the attri-bution process: On the origins and maintenance oferroneous social assessments. In D. Kahneman,P. Slovic, & A. Tversky (Eds.), Judgment underuncertainty: Heuristics and biases. New York:Cambridge University Press, in press.

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Ross, L., & Lepper, M. R The perseverance of be-liefs: Empirical and normative considerations. InR. A. Shweder & D. Fiske (Eds.), New directionsfor methodology of behavioral sciences: Falliblejudgment in behavioral research. San Francisco:Jossey-Bass, in press.

Ross, L., Lepper, M. R, & Hubbard, M. Perse-verance in self-perception and social perception:

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Biased attributional processes in the debriefingparadigm. Journal of Personality and Social Psy-chology, 1975, 32, 880-892.

Ross, L., Lepper, M. R., Strack, F., & Steinmetz, JSocial explanation and social expectation: Effectsof real and hypothetical explanations on subjectivelikelihood. Journal of Personality and Social Psy-chology, 1977, 35, 817-829.

Slovic, P., & Fischhoff, B. On the psychology ofexperimental surprises. Journal of ExperimentalPsychology: Human perception and Performance,1977, 3, 544-551.

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Received August 20, 1979 .