1 Hwnnrr

'nsulting?L1 Hunutr

). (7997).the law,

't1, Public

). (2005).e on juror& K . D .entpirical

rrd Press.T)^ ! l - ^ l -

. / I d t r t a ^ -

). (2000).:cts: Inte-

Lnzt, and

re effectslirniting

d groupBehnttior,

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tpp. 7467

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t 1

C H A P T E R 1 3

Eyewitness Identification Research:Strengths and Weaknesses of

Alternative MethodsGARY L. WELLS ar.ro STEVEN D. PENROD

vEWTTNESS TDENTIFICATIoN RESEARCH has become an increasingly popular

specialty among those interested in psychology and law. We have

tried to write this chapter in a wav that would be useful for new or"would be" eyewitness researchers, and we also think that tl'rere might be

some points here that seasoned eyewitness researchers might find useful. The

reader should keep in mind, however, that that there can be different views

about what is the best methodology for eyewitness research. We offer our best

advice, but that is no guarantee that following our advice will automatically

disarm critics of any researcher's siudy. Furthermore, researchers sl'rould

always consider any particular recommendation that we make in the context

of the hypotheses, purposes, and goals of their own study.

For example, one of the authors of this chapter favors a methodology in

which fillers are counterbalanced in and out of the position of the innocent

suspect rather than having one person always serve as the innocent replace-

ment for the culprit (a general preference of the second author). Both authors

agree, however, that if the purpose of the study is to test ideas about lineup

bias emanating from poor fillers, the counterbalancing methodology wouldnot make sense. We cannot anticipate every hypothesis that researcherswould want to pursue, so researchers will always have to think through

every methodological decision within the context of the questions they aretrying to answer.

Readers should also note that considerations of ecological validitp althoughoften dominant in eyewitness research, can sometimes take a back seat to

theoretical considerations. Consider, for example, the removal-without-

replacement procedure for lineups in which the culprit-absent lineup is createdby removing the culprit and replacing him/her with no one (Wells,1993).

237

238 CnrlrrruaL Lew-Tnral Issurs

From the perspective of ecologicar validity, this is a peculiar methodologywithout much of a real-world counterpart. on the othei hand, this methodJl-ogy is powerful for testing certain types of theoretical questions and is, insome ways, a "cleaner" manipulation of the culprit-present lineup versus ,culprit-absent lineup variable. This is because the traditional methoi (replacethe culprit with someone else) changes t1,o variables at olce (the culprit isremoved, and a new face is introduced), whereas the rernoval-without-replacement procedure removes only the culprit. Depending on the purpossof the study, ecological validity does not alwiys trump other concerns. In fact,the relative paucity of theory developme.t in the eyewitness area is somethingthat many researchers now believe neecls to be rettified, which could lead tothe use of methodologies that are less ecologically valid but more revealing ofpsychological processes (see Applied Cognitiae ps,t1cholog1,2008, Volum eZi$),devoted to such discussions).

Readers should also keep in mind that rnethodological sounclness is on$one factor that determines whether an eyewitness stucty is likely to survivethe rigorous review process and be accepted for publication. Many manu_scripts are rejected from top journals despite their methodological ,ol1dn.r, lbecause the study does not significantly advance o.r, knoirledge. one of ,the poorest reasons to conduct a study is merely that ,,no one has done ir,,All studies have to be justified at much deepei levels than that. why is itimportant? How does it relate to the current literature? How does it aclvanceour theoretical understanding? what are the applied implicatio.s? Noviceeyer'r'itness researchers would do well to examine carefully the introduction ,and discussion sections of r,vell-cited eyewitness articles to develop a feelfor :lror,v these articles were "packaged,.,,

EYEWITNESS IDENTIFICATION LABORATORYEXPERIMENTAL METHODS

Designing, conducting, and analyzing an eyewitness identification experi-ment involves a series of decisions that can have considerable consequencesfor the results and their interpretations. Although we cannot exhaust all thepossible decision junctures that confront eyewitness identification research-ers/ many of which depend o. specifics of the hypothesis being tested, thereare several that confront researchers in the design of almost ill eyewitnessident i f icat ion experiments.

The basic idea of an eyewitness ic{entification experiment is to exposeparticipant witnesses to an event in which they view one or .r.,or" u.tor, ,engaged in some critical behavior. Later, the participant witnesses are given isome type of eyewitness identification test, usuallya photo array, in whichthey are asked to attempt to identify the individual(sj. In most eyewitnesside.tification experiments, the participant witnesses are also asked to indi-cate the confidence or certainty they have in their identificatiol decisions. iDepending on the focus of the experiment, other measures might be taken,

such as dec;their identifand so on.ward. Butsomewhat r

Tss EvsNr

One of the iare many e.events, sucl(see Wells,eyewitnessthe researcLis certainlycontinuingwitnesses irpresentatiotypically hrOn the othrwith videowitness evethat eyewiileaving littlevent rneth

Regardleresearcherstions of theweapon-forand the sangroups (Cl

between th(weapon vrsolved everto Class A r

takes onlyentire classaffects the

For exarspread quirin which tl"randomlysuspiciousappreciabl,the possibi

Jology:hodol-1 ls, ln

versusreplacelprit isithouLrPosesIn fact,rethinglead torling ofe 22(6),

is only;urvivemanu-ndness.One offne it:"hy is itdvanceNoviceluctionfeel for

experi-

luencest all the:search-rd, therelwitness

exPosee actorsre givenn whichlwitnessto indi-

:cisions.'e taken,

Eyewitness Identificntion Research 239

such as decision latency, willingness of participant witnesses to testify about

their identification decision, staiements about how they made their decisions'

and so on. In many respects, such an experiment seems rather straightfor-

ward. But the apparent simplicity of preparing such an experiment is

somewhat decePtive'

THs EvrNr

eu.ntr, such as thefts, in *|rl.h unsuspecting people become eyewitnesses

(see Wells, Rydell, & Seelau, 7993, for an example)' Increasingly' however': - J ^ ^ ^ . ' ^ a f o t L a l

eyewitness iientification researchers have come to rely on video events that

,the researchers create, often depicting some type of crime. uslng video events

i, ...tuirrty easier than using live events, because video does not require

One of the initial decisions to be made is what kind of event to create' There

*. *u"y examples in the eyewitness identification literature of live staged

gontinuing reenactments with actors, there are no concerns about participant

witnesseslntervening to stop the crime, the event is perfectly consistent in its

,presentation frorn or,-e participant to the next, and institutional review boards

iiypicarry have fewe, .on."t.'r about video events :hl iTlt^l1li.ll,l,'i;6i-it.'",n"r hand, it is possible to raise concerns about ecological validity

,with video events due to the obvious fact that eyewitnesses in real cases

witness events live, in three dimensions, and so on. But, at this point, it seems

that eyewitness scientists have largely accepted the video-event method,

,,leauir,g iittle incentive for researchers to use the more difficuit and costly live-

goups (Classes A and B) are nested within conditions. Any differences'tetouu"r, the classes are therefore confounded with the manipulated variable

(weapon vs. no weapon). Surprisingly enough' the problem of nesting is not

solved even if there were 400 itudents and they had been randomly assigned

toClass A or Class B. The reason that this does not solve the problem is tirat it

event method.Regardless of the medium chosen for the witnessed event, we cautron

researchers to avoid designs in which large groups are nested within condi-

tions of the study. At thelxtreme, imagine that a researcher was testing the

, *uupo"-ro.us effect by having a classroom disruptor flash a knife in Class A

, and the same disruptor have no weaPon when disrupting Class B' In this case'

takes only one small glitch (which could easily be undetected) to affect au

entire class (or a large"portion of the class); if something affects the class' it

affects the entire condition.

For example, maybe a student was suspicious' and- a whispering rumor

spread quictty in only one class. Contrast this with a fully randomized design

inwhich the event was staged 400 times, once for each witness, and each was

randomly assigned to the weaPon versus no weaPon condition' That one

suspicious stuJent could affecf only one data point' which would have no

appreciable effect on the condition in which that student fell' Consider also

the possibilitv that the actor who plays the role of the disruptor is unable

240 Cnrvn:el Law-Tnrel Issurs

to enact the event in exactly the same way each time (which is likely).sometimes the actor faces away from the group more than other times, orsometimes the actor moves a little faster. Any minor difference for Class Aversus Class B could impact results for the entire condition (because eachclass is a full condition).

At the other extreme, where each enactment is done for each individualwitness, these minor variations "wash out," because they will occur as oftenin one condition as they do in the other condition (the law of large numbers).Based on strict interpretations of a random design and the assumptionsbehincl statistical analyses, the situation in which groups (Class A andClass ts) are nested in conditions (weapon and no weapon) is the same asan experiment with a total sample size of two (one per condition), not 400(200 per condition). These are extremes, of course, where in the nested. casethere is only one group per condition and in the other case there are nonestings of groups within conditions. Most reviewers and editors will permitsome level of nesting within conditions. For example, groups of two oi threewitnesses at a time are usually not flagged as problematic nestings if theoverall sample size is large enough. Still, researchers need to be prepired forthe possibility that editors or reviewers will require some compliiateh higher-order statistical analyses that are harmful to statistical power when there arenestings. And, at the extreme where there is only one group per condition,there is no statistical solution. Such designs will be (and should be) rejectedfor publication in reputable journals.

once a medium has been chosen for the event, questions arise, such as whatparticipant witnesses are told prior to the event, how long the participantwitnesses will be exposed to the culprit(s), and wheiher to use mulilpleculprits reenacting the same event. Most eyewitness identification researchersuse mild deception to avoid cueing the witnesses prior to the event that theywill witness. For example, in a video-event study, participant witnesses mightbe told that the study involves impressions of people or impressions oferrents. In live-event experiments, participants might be seated in a waitingroom believing that the study has not yet started. The rationale for not alertingparticipant witnesses that they will be witnesses is simply that actualwitnesses are generally iaken by surprise.

The issue of exposure duration is a more difficult one, because the relationbetn'een expostlre duration and eyewitness identification performance is notprecise. The general idea is to find an exposure duration that avoids ceilingand basement effects. An extremely long exposure might result in eyewit-ness identification performance being virtually perfect, which might thenprevent the researcher from showing that certain other variables (e.g., abetter lineup procedure) can improve eyewitness identification perform-ance. Conversely, an exposure duration that is too brief might t"rrrit in sucha weak memory trace that there would be no chance to show how othervariables (e.g., passage of time before the lineup) can harm eyewitnessidentification performance.

The appropriateaspects of the rese;accuracy by militafound that under s<over one in four inlet al., 2004). In co.better performancejust 12 seconds. Hebe done using justperformance to gowe discuss how lir

The question of 'crime, is generaliystimulus samplingcharacteristics of thstudy. For examplothers, in large parappearance than omore important forstimulus samplingtor) variable is an

For example, ifwhen the culpritsampling is essenculprit-actors withprit-actors with miUsing only one or Ithreat) in this case,confounded with t

However, if thestimuli themselvestwo culprit-actorsculprit-actor are tlissues of generalizfrom the manipulencourage readersthese points; it alslessen the need fostimulus sampling

Bunpwc rus LINsut

Great care must beThe need for som,in the lineup, whe

is likely).times, orr Class Aruse each

:rdividualr as oftenrurnbers).umptions;s A and) same as), not 400rsted casere are noill permitr or threergs if thepared forrd higher-there are

:ondition,

) rejected

h as whatarticipantmultiple

searchersthat they

ses might:ssions ofa waiting>t alertingLat actual

e relation.nce is notCs ceilingn eyewit-ight then:s (e.g., aperform-It in suchow otherrewitness

Eyertritness Identification Resesrclt 247

TheappropriateexposuretimeCanvarydramaticallyas'afunctionofoti"reraspects of the ."r"ur.h design' Thus' foi example' a study of identification

accuracybymi l i ta rypersonne lbe ing t ra ined inami l i ta rysurv iva lschoo lfound that under ro*" nigt -stress circumstances, trainees could identify just

.ver one in four interrogiors involved in 40-minute interrogations (Morgan

et al., 2004). ln contrai, M""to", Hope' and Bull (2003) obtained slightly

betterperformancesfromwitnesseswhoviewedatargetpersoninavideoforjust 12 seconds. Hence, pilot testing-is.highly recommended' which can often

be done using just the control conditiorito make sure that there is room for

performancetogoupanddownasafunct ionofothermanipulat ions.(Later,we discuss how lineup performance is assessed')

Thequest io, ,orwn"tnertousemult ipleculpr i ts. ,eachreenact irrgthesamecrime, is generally construed as a" issue of "slimuius sampling'" The idea of

s t imu lussampl ing is toer rsure tha t theres t r l t sarenotdueto thepar t i cu la rcharacteristics of the individual who was selected to serve as the culprit in the

s tudy .Forexample ,weknowthatsomepeop learemorerecogn izab le thanothers, inlargepartbecausesomepeoplehaveamoredist i rrct ive(urrusual)appearance than other people. However, the need for stimulus sampling is

more impor tan t fo rsomestud ies than i t i s fo ro thers . Ingenera l , the issueofstimulus sampling is extremely important when the manipulated (or predic-

tor) variable is an exemplar from a caiegory'

For exampie, if the experiment is exJmining how eyewitnesses perform

when the culprit is Bh& versus white or male versus female, stimulus

sampling is essential. Cleariy, one must comPare many different Black

culprit-actors with *u"y difflrent white culprit-actors or many male cul-

pr i t -actorswithmanyfemaleculpr i t -actorstoreachanyproPelconclusions.Using only one or two such actori threatens construct validity (a very serious

threat) inthiscase,becausethecategoryvariabie(e.g.maleVerSuSfemale) isconfounded with characteristics of the exemplars'

However, if the critical manipulated variatle is not a characteristic of the

stimuli themselves (e.8., a pre-lineup instruction)' then the use of only one or

two culprit-actors i, J ters serious threat, because the characteristics of the

cu lp r i t -ac to rare thesameineachcond i t ion ' In the la t te rcase, therecanbeissues of generalization (i.e., would other exempiars yield the same effects

from the manipulated variables?) but not issues of construct validity' we

encouragereaders toexamineanar t i c lebyWel lsandWindsch i t l (1999)onthese points; it also includes discussions of how statistical interactions can

l e s s e n t h e n e e d f o r s t i m u l u s s a m p l i n g a n d h o w t o a n a l y z e t h e d a t a w h e nstimulus samPling is used'

Butt-otNc ruE LruruP

Great care must be taken in making various decisions about building a lineup'

T h e n e e d f o r s o m e d e c i s i o n s i s o b v i o u s , s u c h a s h o w m a n y p e o p l e t o u s ein the lineup, *huth", to present the lineup live or in photos, and so on. But

242 CnlvrrNnl Law-Tnlnl Issuss

some decisions are even more complex and require considerable foretat a level often not exercised in the eyewitness identification literature. Onethe first decisions to be made is whether to use both culprit-presentculprit-absent lineups. There are circumstances in which using onlyor only absent lineups-is perfectly legitimate, depending on ihe nature ofquestion being asked. Much of the research on the post-identificationback effect, for example, uses only culprit-absent lineups because the focuson the development of false certainty after a mistaken identification hasmade (e.g., Wells & Bradfield, 1998). Using a different rationale (a questithat focused on witness performance in culprit-present arrays), MemonGabbert (2003) used only culprit-present lineups to examine simultaversus sequential lineups. Cenerally, however, if the hypothesiseyewitness identification accuracy, it is critical to use both culprit-presentculprit-absent lineups.

The typical method for creating a culprit-absent lineup is to use thefillers but replace the culprit wiih an innocent suspect. Theoretically,simulates the situation in which police investigators have unknowifocused the lineup on an innocent suspect. But the issue too often gover (or ignored altogether) by eyewitness identification researchers is howselect the person who will replace the culprit (i.e., how to select the isuspect). In some published experiments, researchers state that theya person who closely resembled the culprit. For example, the reseamight sort through a large number of photos, have them rated forto the culprit, and then pick the most similar one to be the replacementthe culprit.

We believe, however, that the choice of strategy should depend onquestions being addressed by the researcher and what one assumesanything) about the ways in which innocent people become suMost often, people do not become innocent suspects in actual casesof their high similarity to the actual culprit. After all, the police invdo not know who the actual culprit is (otherwise they would arrest theculprit instead). Instead, an innocent suspect may be someone who merelythe general verbal description of the culprit that was given by the eyewiBut if the innocent suspect in an experiment is selected a priori to looklike the culprit than do any of the fillers, this can serve to greatly ovethe rate at which the innocent suspects would be identified in actualwhere the innocent person merely fits a general description.

Furthermore, selecting as the innocent replacement someone who loolagreat deal like the culprit could serve to underestimate the conaccuracy relationship. At the extreme, replacing the culprit with a clonethe culprit would yield a result in which it is guaranteed that there can beconfidence-accuracy relation. In the general case of an experiment,recommend a different method than one that selects a person whomost like the culprit as the innocent replacement for the culprit. In parti

way that thI descriPtior

any singl<each of tt

and make thr

peculiarities ait-absent lin,

are other

t closely rences; fo

by a poli,hotographs. I

may bear t

may app.illance vide

the surveillan'uct a lineul

imilarly, a pa dra

witnessesins their stlike. This s

simulatingrate-gull

hers spe'it, we reconparagraPh.h the most-

rate can

the most-sThe issue ofbntification e

aboutselection rr

, the effectsis importan'

tant.In gOne i s '

it (as giveiption fro

i s t o tthe res

ts. (Note

we recommend that the innocent replacement for the culprit be selected ined in

rethoughtre. One ofesent andpresent-ture of the

rtion feed-he focus is

n has been

a questionemon and

rultaneousi concernsresent and

e the same

ically, this

knowinglyen glossedrs is how to

re innocentey selectedresearchersr similarityicement for

end on the

rssumes (if

e suspects.ses becauservestigators;t the actual

r merely fits

eyewitness.o look more'verestimate

actual cases

who looks a

confidence-h a clone of:re can be no

:riment, we

r who iooks

n particular,selected the

Eyezoitness ldentificntiotr Resesrch 243

same way that ihe fillers were selected (often, because they fit the general

verbal description of the culprit). Using this method, there is no reason to

specify any single one of the lineup members as the innocent replacement.

Instead, each of the fillers can be rotated into the replacement position in the

culprit-absent lineup. This type of counterbalancing can help stabilize the

data and make the results more replicable, because the results do not depend

on peculiarities associated with the selection of any single member of the

culprit-absent lineup.

There are other circumstances in actual cases in which an innocent suspect

might closely resemble the actual culprit. Mere chance is one of these

circumstances; for example, a witness may be presented a set of photographs

selected by a police officer-using the witness's description-from a database

of photographs. By chance alone, one of the individuals in this "all-suspect"

array may bear a sirong resemblance to the perpetrator. But other circum-

stances may apply. Suppose, for example, the culprit's image was caught on

surveillance video. As a result, the police might receive a tip that the person

on the surveillance video closely resembles Person X and they might decide to

conduct a lineup with Person X as their suspect.

Similarly, a person could become a suspect because he or she closely

resembled a drawing or "composite" of the perpetrator prepared by one or

more witnesses and published in the media. In this case, the police are

selecting their suspect based on some knowledge of what the actual culprit

looks like. This situation is what many eyewitness identification experiments

are simulating when the eyewitnesses use iheir knowledge of what the

confederate-culprit looks like in selecting an innocent suspect. Unless

researchers specifically intend to simulate this circumstance or something

like it, we recommend the counterbalancing method described in the preced-

ing paragraph. This method can be coupled with a reporting of the rate at

which the most-chosen innocent person was selected by witnesses. The most-

chosen rate can give some indication of the risk of misidentification associated

with the most-similar foil.

The issue of how to select fillers confronts virtually every eyewitness

identification experiment. Obviously, if the experiment itself is testing hy-

potheses about the best way to select fillers, the hypotheses themselves dictate

the selection method. But if the experiment is testing some other question

(e.g., the effects of pre-lineup instructions or the effects of exposure duration),

it is important to remember that the method of selecting fillers is still

important. In general, researchers have focused on two methods for selecting

fillers. One is to select fillers who fit the general verbal description of the

culprit (as givenby people who are shown the culprit and then asked to give a

description from memory), which is cailed the match-to-description method'

Another is to select fillers who show some level of similarity to the culprit

(called the resemblance-to-culprit method) as rated by pilot study partic-

ipants. (Note that how this plays out in any given experiment must be

determined in part by how the innocent suspect is selected')

,1.

r l

:.'.

244 CnrrrarNnl Lnw-Tnrel Issurs

In actual police practices there is jurisdictional variation. Some jurisdictionsselect their fillers based on the verbal description of the culprit that wasgiven by the eyewitness(es). Other jurisdictions select the fillers based ontheir similarity to the suspect. The latter practice (similarity-to-susmethod) is actually different from the way fillers are selected in almostany experiment, because the fillers that are selected are more likely to bedifferent if the suspect is innocent than if the suspect is guilty. In other words,the similarity-to-culprit method is not the same as the similarity-method. Regardless of how an experimenter decides to select the fillers to:be used in the study, it is essential that the method be fully described inany write-up of the study. Furthermore, researchers should usually reportsome measure of the final lineup product. Often, this measure is functionalsize (Wells, Leippe, & Ostrom, 1,979) or effective size and defendant bias(Malpass, 1,987), both of which involve the collection of additional datafrom "mock witnesses." However, it should be noted that these measuresare totally insensitive to a bias that occurs when the innocent suspect isselected to resemble the culprit, whereas the fillers are selected to fit thedescription (Wells & Bradfield,1.999).In such a situation, the functional-sizgeffective-size, anddefendant-bias measures will show no lineup bias, and theinnocent suspect will actually stand out.

REPORTING AND ANALYZING THE DATA

IorNrrRceloN Dnrn

Clearly, there are many different approaches to reporting and analyzing data,from an eyewitness identification experiment, and researchers must always'consider the unique aspects of their experiments in deciding how to approachthe data. Nevertheless, there are problems that reoccur frequently. The mostcommon problem is one of underreporting the data. Too often, for example,researchers will collapse across types of accuracy (e.g., identifications of theculprit in a culprit-present lineup and correct rejections from a culprit-absentlineup) and iypes of inaccuracy (e.g., identifications of the innocent suspect,incorrect rejections when the lineup included the culprit, and filler identifi"cations in both culprit-present and culprit-absent lineups).

Unfortunately, collapsing across both types of accuracy and both types ofinaccuracy masks a lot of interesting and important information. We believe:that any eyewitness identification experiment that includes culprit-present:and culprit-absent lineups should minimally report the descriptive statistics,that are characterized by Table 13.1. This kind of table is useful becauseitexhausts the possible responses that witnesses can make in response to eachlineup type. of course, this sl"rould be done for each condition of the experi.ment and here we have displayed two conditions-X and Y. Note that'reporting both the percentages and the frequencies is important, especiallyif the conditions do not have equal sample sizes. In some cases, it can also be,

,f:

Lineup con

Condition,

Culprit-Pre

Culprit-Abr

Condition

Culprit-Pre

Culprit-Ab

Note: Numl

usefui tidentifit

The {that thethan usmembeThis isreceive20Vo Ginngcetrate di'

The,elewitway tccationin culJ13.1, athe ralquick

AItInostichits (i<innoctratio i

effect,prete(fromculprand t

-rrisdictions'it ihat was's based on-to-suspect

I in almostlikely to bether words,-to-suspect

re fillers toescribed inLally reportfunctional

ndant biastional dataI measuressuspect is

I to fit thetional-size,as, and the

yzing dataust alwaysr approach. The mostr example,ions of therrit-absentnt suspect,er identifi-

-h types ofVe believerit-presente statisticsbecause itse to eachhe experi-Note thatespeciallyan also be

Condition X

Culprif Present

Culprit-Absent

Condition Y

Culprit-Present

Culprit-Absent

65%(52)

Cannot occur

75% (60)

Cannot occur

Cannot occur

10% (8)

Cannot occur

30"/" (24)

157" (12t

50% (40)

5%(4)

20"/. (16)

Eyewitness Identification Resesrch 245

Table 13.1Distributions of ldentification Decisions as a Function of Culprit-present

and Culprit-Absent Conditions and the XYManipulation

Witness lD DecisionLineup condition lD of Culprit lD of lnnocent Suspect lD of F i l ler No lD

20% {16)40% (32)

20% (16)

50% (40)

Nole: Numbers in parentheses are frequencies.

useful to report the rate at which each individual filler in the lineup isidentified rather than collapsing all fillers into one total.

The format of data presentation in Table 13.1 is based on a presumptionthat the design of the experiment used a single a priori innocent suspect ratherthan using the method of roiating the innocent suspect across all lineupmembers (the counterbalancing procedure discussed in the previous section).This is apparent from the fact that the innocent suspect in Condition yreceived 30% of the choices whereas the five fillers in total received only20vo (an average rate of 4vo). rf the rotation method had been used, theinnocent suspect rate of identification would be exactly the same as the fillerrate divided by the number of fillers.

The format of rable 13.1 also permits a quick assessment of whethereyewitness performance is running above levels expected by chance. oneway to define chance is to compare ihe rate of correct rejections (no identifi-cation in culprit-absent conditions) to incorrect rejections (no identificationsin culprit-present conditions). Because the frequencies are reported in Table13.1, anyone can quickly calculate a chi-square value to determine whetherthe rates are significantly different. The format of Table 13.1 also permits aquick assessment of diagnosticity.

Although space does not permit us to give a full treatment of the diag-nosticity statistic, the diagnosticity of a suspect identification is the ratio ofhits (identifications of the culprit) to false identifications (identifications of theinnocent suspect). In the case of Condition X in Table 13.1, the diagnosticityratio is 6.5, and in the case of Condition Y, the diagnosticity ratio is 2.5. Ineffect, the diagnosticity ratio for identifications of the suspect can be inter-preted as how much more likely an eyewitness is to identify the guilty partyfrom a culprit-present lineup than to identify an innocent suspect from aculprit-absent lineup. A diagnosticity ratio of 1.0 indicates no diagnosticity,and higher numbers indicate increasing levels of diagnosticity.

246 CRtr,ttxel Lew-Tulnl IssuEs

The diagnosticity ratio can be also computed for fillers and for

iclentification decisions. Diagnosticity ratios are quite important for

analyses that attempt to use Bayesian siatistics to calculate probabilities

error under different possible base rates for whether the lineup incl

the culprit. Detailed treatments of eyewitness identification diagnosti

and Bayesian probabilities can be found in the eyewitness identi

literatttre (Wells & Lindsay, 1'980; Wells & Olson, 2002; Wells & Turtk

1gSO. The article by Wells and Olson also describes how io test whethel

diagnosticity ratio is significantly different from 1.0 or whether one diag

nosticity ratio is significantly greater than another diagnosticity ratio'

Commonly, researchers first want to know whether the manipulation

conditions X vs. Y in Table 13.1) had any significant effect on eyewi

identification performance. Analyses of variance are generaily not a

ate for data of this form (i.e., categorical data of a dichotomous form).

omnibus (overall) test of staiistical significance is readily available,

using a hierarchical log-linear analysis, which is contained in SPSS and ot

statistical packages. Individual contrasts (e.g., is the 107o rate of in

suspect identifications in condition X statistically different from the 30%

of innocent suspect identifications in condition Y?) are also easily condu

using the chi-square statistic.

CoruRoErlcs Dnrn

Commonly, researchers are interested in using confidence measures to

the relation between confidence and accuracy. The point-biserial correlati

has been the most common method for doing this in the eyewitness i

cation literature, but numerous researchers have quesiioned the appropri

ness of the point-biserial correlation and have instead argued for

of calibration and resolution (e.g., Brewer, Keast, & Rishworth,2002;

& Wells,2006; Juslin, Olson, & Winman ,7996)' One problem is that cali

and resolution statistics require either extremely large sample sizes or a

number of repeated measures per pariicipant. Note, however, that cal

can be calculated properly only if the confidence scale is categorical from

to L00% (i.e., the commonly used 7-point scale cannot be used)'. Furl

cornplicating the traditional practice of reporting the point-biserial

tion between confidence and accuracy is the fact that the point

l. The fact that confidence calibration calculations require 0-100% scales rather than

common scales (e.g., 1-7) might itself be a good reason to use 0-100% confidence sc

eyewitness identification studies. In general, the authors recommend percentage

for confidence questions, because percentage scales have some degree of lay comp

hension and meaning. Hence, percentages might be more natural and readily grasped

participar-rt witnesses. Furthermore, text, figures, and tables in articles that refer to n

confidence levels. such as 3.9, require the reader to go back to the methods section

look again at n'hat kind of scale was used (5 point? 7 point? 9 point?) to get a sense

where participant-witnesses l\rere on the scale. Percentage confidence, on the other hat

does not impose this ambiguitY or extra bttrden on the reader'

1 for no-t for anybiiities ofincludes

gnosticityrtification& Turtle,,vhether aone diag-ratio.rtion (e.g.,

yewitnessappropri-form). Anhowever,and otherf innocente 307o rate

:onducted

rs to assess:orrelationss identifi-rpropriate-'measures

02; Brewercalibrations or a largecalibrational from 0%)1. Furtherial correla-int-biserial

rer than otherence scales in:entage scalesf lay compre-ly grasped byreier to meanls section andget a sense ofre other hand,

Eyeuitness Identification Research 247

Table 13.2Frequency Array for Confidence Level by Accuracy

Accuracv O"/" 10% 20"/" 30% 40"/" 50% 60% 70% 80% 90% 100%!

Accurate

lnaccurate

correlation is sensitive to base rates (McGrath & Meyer, 2006).In the current

context, that means that the base rate for accuracy affects the point-biserial

correlation.Regardless of the summary statistic used to express the relation between

eyewitness identification confidence and accuracy, we recommend that

researchers also consider reporting confidence level using accuracy/

frequency arrays. Table 13.2 gives an example of such an array. This array

is extremely useful because it permits readers to calculate the point-biserial

correlation, or d, or any other statistic. Importantly, it also permits those who

are doing meta-analyses to easily collapse across studies. And, it allows

researchers to explore the idea that extreme confidence (e.g., 90% or more

confident) might be populated almost exclusively by accurate witnesses (in

this case 897o of witnesses with confidence of 90% or better are accurate) even

when the overall distribution shows a modest or weak relation.

It is now well documented thai the relation between eyewitness identifi-

cation accuracy and confidence is consistently moderated by whetl'rer the

witnesses are choosers (i.e., made an identification) or non-choosers (e.g., see

Sporer, Penrod, Read, & Cutler, 1995). Hence, it is not recommended that

researchers collapse over both types of accuracy (accurate identifications and

correct rejections) and both types of inaccuracy (mistaken identifications and

incorrect rejections) when reporting confidence-accuracy relations, because

this can hide the fact that the relation is stronger among choosers (accurate vs.

inaccurate identifiers) than it is among non-choosers (correct rejecters vs.

incorrect reiecters).Finally, we note that researchers should consider the fact that the confi-

dence-accuracy relation in eyewitness identification might also vary as a

function of whether the identification of fillers in the culprit-present lineup

are included among the choosers in calculating this relation. From a PersPec-tive of the ecology of the forensic situation, in actual cases we would not

normally be interested in the question of wl'rether eyewitness identification

confidence helps to discriminate between identifications of a guilty suspect

and identifications of fillers. Using the assumption of the single-susPect

model for lineups (one person is the suspect and the remainder are known

to be innocent fillers), it is already known in an actual case whether the

identification of a filler was mistaken-clearly it was. Instead, eyewitness

identification confidence is useful to the extent that it helps discriminate

between accurate identifications (i.e., when the culprit is present) and mis-

taken identifications of an innocent suspect (i.e., when the culprit is absent).

5 1 0 3 4

1 5 1 5 3 3

0 0 0 2

0 0 1 4 1 2

2 1

1 7

1 7 8

2 1

248 CntvlNel Law-Tnlel IssuEs

In some cases, it might be informative to report the average confidence with

wl'ricl-r every lineup member was chosen; the suspect in the target-present

lineup, each individual filler in the target-present lineup, and each individual

member of the target-absent lineup. If standard deviations are also reported

with each of these L2 means, it would be easy for the interested reader to

calculate the confidence-accuracy correlation under any number of assump-

tions (e.g., if the most-selected filler was the innocent suspect versus the

average filler).Readers should note that many of the points we have made here about

confidence apply as well to other continuous-variable "postdictors" of eye-

witness identification accuracy, such as identification decision latencies.

Again, however, the approach that a researcher takes can vary depending

on the nature of the questions being asked. In the case of decision latencies, for

example, Dunning and Perretta (2002) were interested in finding the number

of seconds that represented the optimum separation of accurate and in-

accurate witnesses. Hence, for their PurPoses it was useful to find the point

along the decision latency time line that yielded the maximum chi-square

value separating the accurate from the inaccurate witnesses.

ARCHIVAL RESEARCH AND FIELD EXPERIMENTS

Although our focus in this chapter has been on ihe design of experimental

studies, it is important to note that other metl"rods have been used to examine

eyewitness performance. Here we consider two forms of research involving

actual cases: (1) archival studies, which use police or prosecutor files to

examine past cases or collect new data in police settings but do not involve

any experimental methods, and (2) field experiments, which use experimen-

tal methods in connection r.vith actual cases. A handful of studies of eye-

witness identification performance in actual cases have made use of archival

records. The largest and best of these studies have been conducted in the

United Kingdom (e.g., Pike, Brace, & Kynan, 2002; Slater,1,994; Valentine,

Pickering, & Darling,2003; Wright & McDaid,1996) and have involved nearly

15,000 eyewitnesses. Archival studies in North America have been much

smaller in scale (e.g., Behrman & Davey,2001; Behrman & Richards,2005;

Tollestrup, Turtle, & Yuille, 7994).

By t'ield experiments, we mean experiments using eyewitnesses to actual

crimes, usually conducted in conjunction with a police department. We are

not using the term field experiment to refer to an experiment involving a

simulated crime that happens to be conducted in the "field" (e.9., on the street

or in a convenience store). (In the latter case, we consider these to be lab

experiments that happen to step outside of the traditional lab and set up a lab

in some other setting.) A superb example of a field experiment is one

conducted by Wright and Skagerberg (2007), in which actual eyewitnesses

to serious crimes were asked critical questions about their lineup identifica-

tion either before or after being told whether the person they identified was

the susPect in tldid not mattersuspect, becaus

If the issue i

and field exPerthe highlY con'Chicago Policelems with thisSteblay, in Prewith the factotwas or was noldefinitivelY knthere is no amlwas accurate cthe identificatiIn all of the I

exampie, the ialbeit an inno

One waY tcexperiments iwhereas thesometimes nidentificationthis strategY {

field exPerim(1994) observbetween misrecorded as ethe same Proto the ChicaPthey were cctrator knew

Of course,is accurate,accurate thathat variabl<tions of fillidentificatioinaccuracY.for instancesusPects anexamPle, coperson is tttheir identi:merelY fiile

nfidence witharget-presentch individualalso reportedted reader torr of assump-:t versus the

e here abouttors" of eye-x latencies.r dependingIatencies, forthe number

:ate and in-rd the pointt chi-square

S

<perimentalto examine

h involvingtor files tonot involve:xperimen-lies of eye-of archivalcted in theValentine,ved nearlyreen muchrrds, 2005;

; to actualnt. We arervolving at the streetto be lab

:t up a labnt is onewitnessesdentifica-lified was

Eyezttitness Identification Resenrch 249

the suspect in the case or merely a filler. In the case of this field experiment, itdid not matter whether the suspect was the actual perpetrator or an innocentsuspect, because the question concerned the effects of receiving feedback.

If the issue is one of accuracy of identification decisions, archival studiesand field experiments present special challenges. This is readily apparent inthe highly controversial field experiment conducted by an employee of theChicago Police Department (Mecklenburg, 2006). The methodological prob-lems with this study are well documented (e.g., see Schacter et al., 2007;Steblay, in press). For current purposes, however, we are more concernedwith the factors that lead to ambiguity regarding whether an identificationwas or was not accurate. In a lab experiment on eyewitness identification, it isdefinitively known whether a suspect in a lineup is in fact the culprit. Hence,there is no ambiguity in a lab experiment as to whether a given identificationwas accurate or inaccurate. In an archival study or field experiment, however,the identification of a suspect might or might not be an accurate identification.In all of the DNA exoneration cases involving mistaken identification, forexample, the identification that was made was the identification of a suspect,albeit an innocent one.

One way to partially get around this problem in archival studies and fieldexperiments is to note that the identification of a liller is always an enorwhereas the identification of a suspect would sometimes be an error andsometimes not. In the UK studies, approximately one in three positiveidentifications made by witnesses was a foil identification. However, eventhis strategy for determining errors can be problematic in archival studies andfield experiments due to poor record keeping. For example, Tollestrup et al.(1994) observed that the Royal Canadian Mounted Police did not distinguishbetween misidentifications of foils and rejections of lineups-both wererecorded as a failure to identify anyone. Behrman and Davey (2001) reportedthe same problem in their study, and it is clear from footnote 3 in an appendixto the Chicago experiment that foil identifications were not recorded becausethey were considered "tentative," at least in conditions where the adminis-trator knew the identity of the suspect.

Of course, even without knowing whether the identification of the suspectis accurate, one can assume that such an identification is more likely to beaccurate than is the identification of a filler. In this sense, it could be arguedthat variables that increase identifications of suspects or decrease identifica-tions of fillers are promoting accuracy, whereas variables that decreaseidentifications of suspects or increase identifications of fillers are promotinginaccuracy. Still, great caution must be exercised in using this logic. Consider,for instance, the myriad \^rays that one might increase identifications ofsuspects and decrease identifications of fillers in a field experiment. Forexample, comparing a condition in which witnesses are keptblind as to whichperson is the suspect with a condition in which witnesses are told prior totheir identification decision which person is the suspect and which ones aremerely fillers. The latter would serve to depress the identification of fillers and

250 CRnrrxel Law-Tnrel Issurs

increase identifications of the suspect. Surely we would not accept thisevidence that witnesses should be told which person is the suspect andare fillers.

r e ma

Alternatively, consider what happens if the fillers in the lineup are vant;specifically to be implausible lineup members (e.g., do not fit the wi fieldescription of the culprit). That would also serve to depress filler identi queltions and increase identifications of the suspect. But does thataccuracv? As a final example, if the depression of filler identifications is agood outcome, then why use fillers at all? why not make every lineup a showup instead? The point here is that it is not automatically true that variathat decrease filler identifications or increase suspect identifications inexperiments necessarily promote accuracy (Wells, 2008).

Similar problems can emerge when examining the confidenceExPtrelation in archival and field experiments. Again, the idea is that

identifications are definitely inaccurate whereas identifications of sushave at least some (perhaps the most) accurate identifications in the mi numl

q o" -

ircr(tr'

ysCin

ence the confidence of the witness based on the lineup administr their

Hence, the relation between eyewitness identification confidence andfiller versus suspect identification decisions can be a proxy for the confideaccuracy relation in field experiments. Caution must be exercised herewell, because there is compelling lab-based evidence that non-blind liadministrators (who are the ones soliciting the confidence staiement) i

knowledge of whether the witness identified a filler or the suspect (see Carrioch & Brimacombe, 200i). Hence, in any iurisdiction in which

should be the one who administers the lineup.Finally, we note that field experiments also differ from lab experi

in numerous ways that increase the need for quite large sample sizes. Inexperiments, for example, it is possible to give all witnesses the sameand quality of view, the same duration of exposure, the same delay betweenwitnessing and testing, the same fillers, and approximately the same levelsanxiety, fear, arousal, and so on. In a field experiment, in contrast, thesenumerous other variables float freely and vary widely from one witnessthe next. Careful measures of these free-floating variables can help at thelevel of data analysis if they are statistically controlled, but in geneial, theyrcontribute noise to the data that results in the need for larger sample sizesthan are needed in the typical lab experiment.

rESS

TTNESS

reveale,mPl

&Messtrr

Daco.

made tthat theare wr(

W e ts o f

have b,and strMemor

,and fie,witness

as a prl'correct

weaportobberl

lineup administrator is the case detective or someone who knows whi ith 71person is the suspect and which ones are fillers (which is the case injurisdictions in the united states), the relation between witness confi

noor confidence of witnesses should routinely use double-blind proced lil(wells, 2008). This means that neither the case detective nor any exP€individual who knows which members are fillers and which is the suspect

and whether the witness picked a filler instead of the suspect is likely toartificially inflated by the lineup administrators' influence on the witness, alenti

In general, field experiments that are designed to examine the acc

this asI which

;elected'itness's

:ntifica-rromote

>ns is aa show-lriablesin field

rcuracyrt filleruspectsre mix.rnd theidence-nere aslineup

) influ-trators'' t ( p o_ - r _ . b . /

ich thewhich

n mostfidencey t o b etnCSS.

rcuracy'edures

' other;uspect

'iments

. In labre typeItweenrvels ofrse andness toat the

Ll, theye sizes

Eyezuitness Identification Research 251

GENERALIZING RESEARCH FINDINGS

Our emphasis in this chapter has been on experimental methods. We have

noted a number of the strengths of experimental methods and some of the

advantages of laboratory and staged-event experiments over archival studies

and field experiments involving actual cases. Our emphasis naturally raises

the question of whether the results from laboratory and staged-event experi-

ments generalize to real-world witnesses and what evidence rt'e might use to

address that question. Although space does not permit us to undertake a full

review of relevant research findings, we do wish to highlight some of the

ways in which the question can be addressed and note a few examplefindings.

Do ExpEnnurENTAL STuDIES AND SruDIrs WnH Acruel

Wnrunssrs YiEr-o CoNvERcENT Fwnntcs?

A number of archival researchers have endeavored to test whether findings

revealed in experimental studies are replicated with actual witnesses. For

example, laboratory studies indicate that the probability of identifying a

perpetrator is reduced by the presence of a weapon (e.8., E. F. Loftus, Loftus,

&Messo, 7987;Maass & Kohnken,7989), and Steblay Q992) reported a reliable

impairment from the presence of a weapon in a meta-analysis of 19 studies.

In their archival study, Tollestrup et al. (1994) found that the presence of a

weapon reduces the likelihood of the suspect's being identified: 47Vo of

robbery suspects in cases involving a weapon were identified, as compared

with 7L7o of suspects in robberies without a weapon. In contrast, Behrman

and Davey (2001) found similar rates of identification of police suspects when

they compared240 witnesses to crimes in which a weapon was used with 49

witnesses in crimes without weapons. In their study of 640 witnesses,

Valentine, Pickering, and Darling (2003) found that the presence of a weapon

had no effect on the likelihood of identifying a suspect, but witnesses were

more likely to identify a foil if a weapon was not present. Similar comparisons

of experimental and archival findings involving other variables have been

made by Valentine et al. along with others, and it is not uncommon to see

that the findings do not converge. Does this mean the experimental findings

are wrong?We believe it is entirely too early to reach any conclusions from compari-

sons of this kind. Certainly there is little doubt that a great many variables

have been shown to reliably affect witness performance using laboratory

and staged-event experimental methods (see, e.g., the review by Wells,

Memon, & Penrod, 2000. However, archival and field-experiment data suffer

from a number of deficiencies. As we have noted previously, archival studies

and field experiments generally cannot authoritatively establish whether

witnesses have made correct identifications. They rely on suspect choices

as a primary variable, and because suspect choices can involve a mixture of

correct and incorrect identifications, researchers should not be too surprised

:l

252 CnlvrN,ql Law-Tnnl Issurs

to observe a different pattern of results when they compare such studies withresults from experiments in which accuracy is known.

Another important difference between experimental studies and fieldarchival studies is that field and archival studies cannot easily isolatevariables, because those variables are correlated with other variamany of which might not have even been measured. Consider, for example;,a field study that involved numerous witnesses to a shooting in which it wasfound that those who were most stressed by the shooting were the moslaccurate in reporting details of the event (Tollestrup et a1.,1994). This findingseemingly goes against the general consensus of the experimental literaon stress and accuracy. However, a closer examination of the data also showsthat witnesses who were physically closest to the shooting were the moslstressed (which makes sense), and those closest to the event had theview and were more accurate. These are called multi-collinearity problems,and they are rampant in field and archival studies, which makes it difficulttoreach conclusions about the role of individual variables.

There are certainly other features of field data that can muddy the resultsfrom such studies. Consider, for example, that in field studies it maydifficult to determine whether a weapon was actually visible to a witnessfor how long. In addition, not all witnesses are necessarily tested whenpolice have a suspect. Witnesses who report a poor memory (those who sawweapon?) may indicate that they do not really remember what the perpelooked like and might, therefore, not be shown a suspect. Furthermore,might ask about case "selection" effects. Are the police differentially selectiweapon versus non-weapon cases for more intensive invesiigation (we

so)? Does more intensive investigation of weapons cases yield a highuproportion of guiity suspects (and a higher proportion of suspect choias compared with non-weapons cases? We do not know the answer toquestions, though they are subject to research.

Do DrrrenrNr Rrsrencu MEruoos PnooucE DrrrunrNr Rrsulrs?

As we highlighted earlier in this chapter, researchers are confronted with avariety of methodological choices when they construct their research studies,giving rise to the following questions:

Should a long or short video be used rather than a staged eventcontaining one or several culprits?Should the culprit be replaced with a look-alike when making culpritabsent arrays?How many fillers should be selected and in what manner?Do these choices yield differences in results that might prompt us toconcerned about the generalizability of our findings?

We would poini to two types of analysis that address the question.

a

ShapircI ider

reported ithe studittions werrthe studi<studies ofions, sucl

iticexl

tory stuizable acr

Similarcomparecthat the owas signi

false athan twomade fro

Althoumore rea.

II

res waI)

Shapiro 'explain Ivariablesan upcolcontribut(numberperform;(facial revarrance

A secoby PenrraPpearec

mit c<over stucinteract '

rneta-an;lve varli

listicuentii

itne

-udies with

nd field or;ily isolate

variables,,r example,hich it was: the mosthis findingI literaturealso shows: the mostthe betterproblems,difficult to

the resuitsit may bewitness orwhen the

who saw a,erpetrator'more/ oney selectingr (we hope

a higher:t choices):r to those

:ed with a:h studies,

5ed event

rg culprit-

>t us to be

tion.

Eyetuitness ldentit'icatiort Resenrclr 253

Shapiro and Penrod (1986) published a meta-analysis of factors influencing

facial identification. They drew on results from over 190 individual studies

reported in 128 articles on face recognition and eyewitness memory. Overall,

the studies contained 960 experimental conditions under which identifica-

tions were made and included more than 16,950 participants. Most (80Vo) t>f

the studies analyzed by Shapiro and Penrod (1986) were laboratory-based

studies of facial recognition rather than of more realistic eyewitness simula-

tions, such as videotaped or staged events. They noted that type of study (face

recognition vs. eyewitness) accounted for 35% of the variance in performance

across experimental conditions. Performance levels were higher in the labo-

ratory studies, which raises the question of whether the results are general-

izable across research methods.

Similarly, Lindsay and Harvie (1988) conducted a meta-analysis that

compared a sample of face recognition and staged-crime studies. They found

that the overall correct identification rate (.64) in 113 face-recognitior"r siudies

was significantly higher than the rate (.58) in 47 staged-crime studies and that

the false alarm rate (.18) in 64 face-recognition studies was significantly lon'er

than two types of mistaken identifications in siaged-crime studies-those

made from 47 target-present arlays (.29) and 12 target-absent arrays (.41).

Although these comparisons of laboratory-based face recognition and

more realistic eyewiiness studies initially may seem to raise concerns about

external validity, the difference in performance between the two types of

studies would not raise such concerns if explained by variables (e.g., retention

interval) that generally differ in face-recognition versus eyewitness studies.

Shapiro and Penrod (1986) tested whether "study characteristics" might

explain the differences in identification accuracy rates. They found that

variables associaied wrth nttention variables (including knowledge about

an upcoming test and mode of presentation) made significant individual

contributions. The durntion of exposme per face, Plse, ftletnory load nt sfttdtl

(number of faces studied), and retention interunl accounted for differences in

performance. Once all those variables were accounted for, the type of study

(facial recognition vs. eyewitness) accounted for jtrst 37o of performance

variance (rather than 35%).A second way to address the generalizability issue was addressed in detail

by Penrod & Bornstein (2007), who examined meta-analyses that have

appeared since Shapiro ancl Penrod's (1986) study. These later meta-analyses

permit comparisons of performance across research methodoiogies that vary

over studies; these meta-analyses often ask whether methodological variables

interact with subsiantive variables. Penrod and Bornstein show that these

meta-analyses consistently demonstrate that whenever the effects of substan-

tive variables vary across research methodologies, they are larger for more-

realistic procedures. Factors such as lineup presentation (simultaneous vs.

sequential), weapon focus, stress, live versus video testing, instructions to

witnesses, cross-race identifications, and the like exert larger effects on

eyewitness performance when testing conditions more closely match real

eyewitness researchers failing to consider some of these issues, and neither tion. ,for

254 CRrrurNal L.qw-Tnlel Issuss

witnessing conditions (e.g., staged crime or other eyewitness event and li

video stimuli) than when the situation is relatively contrived and

This pattern of results suggests that if there is a generalizability issue, it ismuch eyewitness research underestimates the magnitude of effects

studied. Based on research to date, researchers and practitioners can

reasonably confident that experimental findings generalize to real e

situations.

CONCLUDING REMARKS

In this chapter, we have described a number of methodological issuesconfront every researcher who designs and conducts an eyewitness i

cation study. In many cases, researchers fail to think these issues throughand end up learning the hard way by having their manuscripts rejectedmethodological grounds or discovering the problem later and having to

the study.We think this chapter might be especially useful for novice

researchers. Sometimes we are surprised, however, to find even ex

the authors of this chapter can claim to be fully exempt from having

bad call on one of these methodological issues- No study is perfect,research involves a constant process of improvement'

We also want to emphasize that with only a few exceptions, ourmendations in this chapter are not universal rules applicable to all sResearchers need to consider the issues we have raised in the context of

hypotheses and goals. We gave examples of some instances of this sort,

as when it is acceptable to use only target-present or only targetlineups. However, when the question being tested is purely theoretical,of the ecological validity considerations can become moot.

Finally, we encourage would-be eyewitness identification researchers

read the eyewitness identification literature carefully to gain a sense of

methodological issues that are often unique to a given study. But, we cauti

researchers not to assume that a study is devoid of all possiblelogical problems merely because it was published. The standards forodological soundness in eyewitness identification research and com

of reporting are higher today than they were only a few years ago, andtrend will undoubtedly continue.

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