The costs of wrongful-discharge laws

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THE

COSTS

OF

WRONGFUL-DISCHARGE

LAWS

David

H.

Autor

John

J.

Donohue

III

Stewart

J.

Schwab

Working

Paper

02-41

November

18,2002

Room

E52-251

50

Memorial

Drive

Cambridge,

MA

02142

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paper

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Science

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Collection

at

The

Costs of

Wrongful-Discharge

Laws

David

H.

Autor

MIT

Department

of

Economics

and

NBER

John

J.

Donohue

III

Stanford

Law

School

and

NBER

Stewart

J.

Schwab*

Cornell

Law

School

November

18,

2002

Revised

from

July

200

1

Abstract

We

estimate the effects

on

employment

and

wages

of

wrongful-discharge protectionsin theUnited States.

Over

thelastthreedecades,

most

U.S.statecourts

have

adoptedoneor

more

common

law

wrongful-dischargedoctrinesthat limitemployers' discretiontoterminateworkersat-will.

Using

thiscross-state

variationwith a difference-in-difference

framework,

we

findrobustevidenceofa

modest

negativeimpact

(-0.8to-1.6 percentagepoints)of

one

wrongful-dischargedoctrine,the implied-contract exception,

on

employment

topopulation rates in statelabormarkets.

The

short-term impactis

most pronounced

for

female,younger,

and

less-skilledworkers,whilethelonger termcostsappeartobe

bome

by

olderand

more-educated workers

-

those

most

likely tolitigateunderthis doctrine.

We

find

no

robust

employment

or

wage

effectsof

two

otherwidely recognized wrongful-dischargelaws: thepublic -policy

and

good-faith

exceptions.Publishedfindingsintheliteraturerange

from

no

effect toverylargenegativeeffects.

We

reanalyzethe

two

leading studies

and

findthediscrepanciescan be explained

by

methodological shortcomings inthe onecase

and

limitations inthecoding

of key

courtdecisionsinthe other.

We

areindebtedtoJoshuaAngrist,DavidCard,LawrenceKatz,AlanKrueger,

Thomas

Miles,

Andrew

Morrissand

seminarparticipantsatthe

NBER

LaborStudies

Summer

Institute,

UC

Berkeley,

NYU

Law

School, Stanford

Law

School,andtheAmerican

Law

andEconomicsAssociationforexcellentsuggestions.

We

gratefullyacknowledgethe

excellentresearch assistanceof Rashida

Adams,

Michael Anderson,SimoneBerkowitz, SarahBernett,Douglas

Bosley,CraigEstes, RoseFrancis, ScottHemphill, Carolyn

Heyman,

Joshua Linn,JoshuaMayes,Marci Reichbach,

What

isthe priceofprotection?Thispaperestimates thesocial costs, in termsofpotentially lower

employment

and

wages,of

common

law

effortstoprotect

American workers from

wrongful-discharge.

The

costof

employment

protectionisa controversial issue. Itisvirtuallyreceived

wisdom

thatthe stagnant

employment

performance of

many

European economies

duringthe 1980s

and

1990s

-

'Eurosclerosis'

-

can

be

attributed tothe significant

employment

protectiongiven

European workers

(cf,Lazear, 1991;

Blanchard

and

Wolfers, 1999).

According

to this argument,

employment

protectionisa double-edged

sword. Itprovides

employment

securityto

incumbent

workersbut

makes

employersreluctanttohire,

leadingtoa stagnant labor

market

withpotentially lower

employment

and

wage

levels.

Among

the

obstaclestotesting thishypothesis isthedifficulty inobtaininghighqualitydata forcross-country

comparisons.

Inthispaper,

we

studytheimpacts

of

employment

protection in theU.S. setting. Several scholars

have

examined

the effectsof

American

federal

employment

laws

on

employment

and

unemployment.

Acemoglu

and

Angrist (2001)

and DeLeire

(2000)presentevidencethatthe

Americans

withDisabilities

Act

decreased

employment

ofdisabled persons.

Oyer

and

Schaefer(2000, 2002) concludethatthe federal CivilRights

Act

of

1991 increased thefrequencyof

mass

layoffs

and

raised the returnstoexperienceforworkers

who

have

a

downward

sloping'age-litigation' profile.

Harm, Todd,

and

van

der

Klaauw

(2001)also evaluatethe costs

of

federalanti-discriminationlaws.

A

major

hurdleforeach ofthese studies isthatthe federal statutesat

issueapplyall atoncetotheentirecountry. Itisdifficulttoseparate theeffects

of

thestatute

from

all other

changesoccurringatthattime(cf,

Donohue,

1998;

Donohue

and

Heckman,

1991).

Thispaper

overcomes

some

ofthesemethodological challenges

by

evaluating

employment

protections

that arise invariousU.S.statesatvarious times, thusprovidinggreater variationwith

which

to

more

accurately establish causalrelationships.

The

UnitedStates,uniquely intheindustrialized world,has long

had

alegal presumptionthatworkers can be fired "atwill"

-

thatis, for

any

time

and

for

any

reason,

good

or bad. Inthelast

two

tothreedecades,however,

most

state courts

have

adopted

one

or

more

common

law

'wrongful-discharge' protectionsthat

weaken

theemployment-at-will presumption. Statesvarygreatlyin

and

Rhode

Island

-

have

neveralteredthe

employment

atwill doctrine.

Ten

states

now

recognize each

of

threebroadclassesof exception totheat-will doctrine:theImplied-contract, Public-policy,

and

Good-faith

exceptions(theirprecise

meaning

isdefined below).

A

few

states

have

rejected prioradoptions(see

Appendix

Table 1). Thisvariability inthe extentand timing ofstates'recognition of wrongful-discharge

laws allows forempiricaltestingoftheirimpacts

on

employment

and

wages.

We

arenot thefirsttoexploretheseeffects.In a widelycited lineofresearch, Dertouzos

and

Karoly

(1992

and

1993) used aninstrumental variables

framework

totest

whether

wrongful- discharge laws

affected state-level

employment.

They

found

surprisingly large impacts.Dertouzos

and Karoly

estimatethat

statesadoptinga tort-based causeofaction(thatis,

one

in

which

plaintiffs

may

sue

employers

forpunitive

damages)

suffered a 3 percent reduction inaggregate state

employment

-

roughlyequivalenttoa

10

percent

employer

sidetax

on

wages

-

with anadditional 1 or2percent

employment

declinefor states alsoadopting

a contract-based protection(that is,

one

in

which

plaintiffs

may

sue onlyfor

economic

losses).

2

These

findings

have

not

gone

unchallenged.Morriss (1995)criticized Dertouzos

and

Karoly's legal variables.

More

recently,

Thomas

Miles (2000) used adifferences-in-differences approachtoestimate theimpact

of

thewrongful- dischargedoctrines.

He

reports

"no

statisticallysignificant effects

on

either

employment

or

unemployment,"

butdoes not

comment

on

thesource

of

the discrepancy

between

hisfindingsandthose

of

Dertouzos

and

Karoly.3

Our

paperjoinsthisdebateat

two

points.First,

we

provide a

comprehensive

reevaluationoftheimpacts

1

To

date,only

Montana

(in 1987) has passeda statuteestablishingagood-causestandardforallemployment

terminations. All otheremploymentatwillexceptionsare

common

lawdoctrines,i.e.,case law. In 1991, theUniform

Law

Commissioners proposeda

Model

Employment

TerminationActsimilartothe

Montana

statute,butnostatehas

yetadoptedit. In 1996, theArizonalegislaturepassed astatuteaffirmingemploymentatwill. Krueger(1991) provides

aperceptiveeconometric study oftheconsiderationof exceptionstothe doctrineofemploymentat willbystate legislatures.

2

Dertouzos and Karoly (1988)earlierexaminedthedirectcostsof wrongful-dischargelitigation inCalifornia.They

foundthesedirectcoststobemodest,amountingtosome $100per termination.SeealsoDertouzosand Karoly (1992;

p. xi)(presenting findingsof 1988study). 3

Inrelatedwork,Kugler andSaint-Paul(forthcoming)findthat a state'sadoptionof wrongful-dischargedoctrines significantlyslowsthejob-to-jobflows ofunemployedrelative toemployedworkers.Autor(2003 forthcoming)and

Miles (2000)findthatemployersincreased

demand

fortemporary helpagencyemployment

when

states adopted

of

wrongful-dischargedoctrines

on

employment

and

wages

usingricher data

and

(we

believe) a

more

complete coding ofthe case

law

than previouswork. Second,

we

evaluate

why

the leading papers

on

this

topic

have

reachedopposing conclusions

-

ranging

from

no

effect tovery largenegativeeffects

-

and

provide a reconciliationofthese findings.

As

withthe Miles

and Dertouzos

and

Karolystudies,our

key

explanatoryvariables are theprecedent

setting casesthatestablish thewrongful-discharge laws recognizedineachstate

and

timeperiod.

We

differ

from

previousstudies, however,

by

usinglegal

and

employment

dataobservedat

monthly

intervals,

by

measuring

wage

aswell as

employment

impacts,

and

by

exploringtheseimpactsseparately

by

education

and

gender

demographic

subgroups overthenear

and

longerterm.

We

applyrobustestimationtechniques

throughout

and

testtheconsistency

and

generalityof ourfindings across specifications

and

timeperiods.

Although

we

had

anticipatedthatourreanalysis

would

reconfirmthenullhypothesis accepted

by

Thomas

Miles,

we

instead finda

modest

but robustlynegativeimpact

of one

wrongful-dischargedoctrine

-the Implied-contractexception

-

on

the

employment

topopulationrate in statelabormarkets. Thisimpact,

which

averages-0.8to-1.6percent,ispresentforal education

and

gendergroups,andis detectable

among

statesadoptingatseveral timeintervalsduringthesample.

The

shortterm impactis

most pronounced

for

females,and

younger and

less-educatedworkers.In thelongterm,however,the costs ofimplied-contract

protection appeartobe borne

by

older

and

more-educated

workers

-

those

most

likelytolitigate.

We

alsofind

some

evidencethattheGood-faith exceptionreducedstate

employment

levels

by

asimilar

magnitude,butthis evidenceisfar lessrobust. Finally,

we

findthatbothdoctrines (Implied-contract

and

Good-faith)

have

a

weakly

positive associationwith

wages

-

thatis,observed

wages

of

employed

workers

tendtorise

by

0.5to 1.5percentagepointsafteradoption ofthese doctrines.

One

interpretation

of

this

findingisthat

employment

protection strengthens

worker

bargaining power, leadingtohigher

wages

and

lower

employment

levels(cf.,

Blanchard

andPortugal, 2000).

However,

a

more

parsimonious explanation

that

we

favor-

and

provide

some

evidencetosupport)

-

isthatthe negative

employment

impacts

of

the

wrongful-discharge lawsareborne

by

thelowest-wage workerswithingiven

demographic

groups, leading

To

reconcile thesubstantialdiscrepancies

between

ourfindings

and

the priorliterature,

we

reanalyze

the

work

ofDertouzos and

Karoly

(1992)

and

Miles (2000).

We

find thattheexceedinglylarge

disemployment

effectsestimated

by

Dertouzos

and Karoly

-

threeto fivetimesthe

magnitude

of our

estimates

-

appeardriven

by

problematicinstrumental variablesthatare spuriously correlatedwithregional

employment

trendsthat substantiallypredate states' adoption

of

wrongful-dischargelaws.

By

contrast,the

differences

between

ourfindings andthose

of

themethodologicallysimilarMiles'sstudyareprimarily

explained

by

discrepanciesinthecoding of

key

courtcases.

By

making

warranted modificationstothese

analyses,

we

demonstratethatthese priorresults

may

bereconciledwith our

own.

I.

Wrongful-discharge

laws

A.

Common

law

exceptionsto

employment

atwill:Definition

and

legal significance

Sincethe

heyday

of

employment

atwill inthe early part

of

the

20

thcentury,legislatures

and

courts

have

restrictedemployers' discretiontoterminate

workers

at-willinseveralways.

Broad

federal statutesprohibit

employers

from

firingworkers

on

the basis

of

unionactivity,race, color, religion, sex, nationalorigin,age,

ordisability. Specific federal

and

statestatutesprevent

employers

from

terminatingworkersfora varietyof

preciselydefined impermissiblereasons, suchastoavoidpensionbenefits

from

accruing, orto retaliate

because a

worker

reportedoccupationalsafety

and

health violations orservedasajuror.5

Inadditiontothese statutoryrestrictions, statecourts

have

overthelast

30

years substantiallymodified

the

employment

at-willdoctrine.

These

modifications,

which

we

refer toaswrongful-dischargelaws, are

commonly

classified inthree categories: (1)thetortof wrongful-dischargeinviolationofpublic -policy

('Public-policy exception'); (2)theimplied-in-factcontractnottoterminatewithout

good

cause

(Tmplied-contract exception');

and

(3)theimpliedcovenanttoterminateonlyingood-faith

and

fairdealing

('Good-National LaborRelationsAct§ 8(a)(3),29U.S.C. §158(a)(3)(enacted 1935)(prohibitingdiscriminationonthe basis

ofunionstatus); TitleVIIofthe CivilRightsAct of1964,42U.S.C. §§2000e to2000e-17 (prohibitingdiscrimination

onthe basisofrace,color, sex, religion,ornationalorigin);

Age

Discriminationin

Employment

Actof1967,29

U.S.C.§§621-634;AmericanswithDisabilitiesActof 1990,42U.S.C. §§ 12101

-

12213.

EmployeeRetirementIncomeSecurityActof1974 § 510,29U.S.C.§ 1140(prohibiting discriminationagainst

employeesbecause theymightobtain benefitsinapensionorwelfareplan);OccupationalSafetyand HealthActof

1970§ 11,29U.S.C. 660(c) (prohibiting discrimination againstemployeesexercisingrightsunder

OSHA);

New

York

faith exception').

We

define these inturnanddiscusstheirsignificance.

As

of1999,allbutsevenstatesrecognized thetortof wrongful-discharge inviolation ofpublic-policy.

Classic violationsofthis 'retaliatorydischarge' doctrine includefiringaworkerforrefusingtoperform an

illegal act, suchas perjuringhimself

on

behalf

of

the

company;

forexercising a statutoryright, suchas

filingaworkers'

compensation

claim; orforperforming a public obligation,suchas serving

on

ajury.

As

Schwab

(1996)discusses, courtstendtoapply thisexceptiontotheat-will doctrine

when

thetermination

clearlyaffects third parties,therebyjustifyingthe judicial interferencewiththeat-will

employment

contract.

Successfulplaintiffscan recover

compensatory

damages

for lostearnings, aswell as

damages

forpain

and

suffering,

and

punitive

damages

inappropriate cases.

Because

thepublic -policyexceptioniswidely recognized (43 states)

and

providesforfull

compensatory

andpunitivedamages, itis

sometimes

viewed

as the

most

significantexception tothe at-will

doctrine. Inpointoffact,however,successful public-policy

cases-

particularlythose withmulti-

million-dollar

judgments

-

arerare, albeithighly publicized.

The

reasonfor their rarityis thatcourts

have

typically

limited thescopeofpublic -policycasestoclear violations of expresslegislative

commands

(e.g., thedutyto

perform juryservice, theright to fileaworkers'

compensation

claim) ratherthanviolationsofavaguer

senseofpublic interest.

Some

legal scholars

have

argued accordinglythatthe attention giventhisdoctrine

inthepopular

and

businesspressexceedsitslegal

and

economic

significance (see

Edelman

et al 1992).

Only

1 1 states

now

recognize aseconddoctrine,thecovenant ofgood-faith

and

fairdealing.6

A

classic

illustration ofthis exception isthecase of

Fortune

v.National

Cash

Register Co. in

which

the

employer

firedasalesperson

who

had

completed a substantial salejustbeforehis

commission

was

due.

The

court

ruledthatthe

employer

had

deprived theplaintiff

of

the"benefitofhisbargain"in

bad

faith. Likethe

public-policyexception, the good-faith doctrine

could have sweeping employer

consequences. Inits

broadestform,thisexceptioncan beread as a general prohibition againstterminating

any worker

for

any

reasonotherthan 'justcause'

-

thatis,

economic

necessity orpoor performance.

Most

courts,however,

have

limited application ofthegood-faith exceptiontogrossly unfair 'timing' casessuch asFortune,

where

thetermination deprives the

worker

ofaspecific

promised

benefitsuchasasales

commission

oran

imminently-vestingpension.

Hence,

the onus

of

thisdoctrineisprobably

somewhat

lessthan

was

originally anticipated

by employers and

legal scholars.

Finally,43 statesrecognize athirdexception to

employment

atwill,theimplied-contract doctrine. This

exceptionarises

when,

through

words

oractions, an

employer

implicitlypromises nottoterminate a

worker

without

good

cause.

A

landmark

decisionestablishingthisexception

was

the

1980

caseof Toussaintv. Blue

Cross

&

BlueShield, in

which

the

Michigan

Supreme

Court heldthat

an

employer'sindirectstatements

aboutthe

manner

in

which

it

made

termination decisionscancreatelegallybinding

employment

contracts9

InToussaint, theplaintiffsuccessfullysuedforbreach ofcontract

by

citinganinternalpersonnelpolicy

handbook

indicating thatit

was

Blue

Cross'spolicytoterminate

employees

onlyfor justcause.

Although

Toussaint

was

unaware

ofthe

handbook

when

hired,thecourtheldthatthe

handbook

impliedabinding

contract. Courtsin

23

otherstatesissued similardecisionsoverthenext5 years.

An

equallyinfluential 1981 Californiacase,

Pugh

v.See'sCandies, further

expanded

the

implied-contractnotion

by

findingthatworkersareentitledto

ongoing

employment

evenintheabsence

of

written

statementsifcontractualrights areimplied infactthroughthecontextofthe

employment

relationship.10

Thiscontext

may

include longevity ofservice,a history of

promotion

orsalary increases, general

company

policies asexemplified

by

treatment

of

otheremployees,or typical industrypractices. Cumulatively, these

court decisionsgeneratedsubstantialuncertaintysurroundingtermination, resultingin

numerous

cases

7

364 N.E.2d 1251 (Mass. 1977). 8

WhileFortunedidnotreachtheissue,

some

statecourtsallowtortdamages(including punitive) forbreachesofthe

good-faithcovenantinemploymentcontracts.Duringour period ofstudy,Californiarecognizedabroadersetof

good-faithobligationsthatishardtodistinguishfromageneral obligationnottofirewithoutgoodcause.Theleading CaliforniacaseisFoleyv.InteractiveDataCorp.,765P.2d373 (Cal. 1988),inwhichabank employee wasfiredfor reporting toupper

management

thattheFBI wasinvestigatinghisimmediatesupervisorforembezzlement fromaprior

employer.Thecourt declaredthesefactscouldamountto abreachofthecovenantof good-faith andfairdealing, but

heldthatonlycontractdamages,notfulltortdamages,wererecoverable. In

Guz

v.BechtelNational,Inc., 8P.3d 1089

(Cal.2000),afterourperiodofstudy, thecourt restrictedgood-faithclaimstothoseliketheFortunecase.

9

292 N.W.2d. 880(Mich. 1980).

10

where

courtsfoundthat

employees

heldimplied-contractual

employment

rights thatemployers

had

not

subjectivelyintendedto offer.

The

employer

costsofthe implied-contractexception are difficult to assess,however. Since

implied-contractcases leadonlytocontractual

damages

(e.g.,punitive

damages

are excluded), thethreatofa

spectacularjury

award

islow. In addition, an

employer

canpotentially insulateitself

from

implied-contract

claims

by

rewriting

employment

contracts

and

handbooks

toclearly state thatall

employment

contracts are

at will.

'

'

However,

unlike thepublic-policy

and

good-faithdoctrines,

which

penalize individual instances of

unethical

employer

behavior, theimplied-contract doctrinecan pervasivelyaffectan employer's personnel

practices.

By

imbuing employer

handbooks

withthestatusoflegal contracts,theimplied-contract doctrine

hasthe potentialto reclassifyan employer's entireworkforceas notatwill,causingthe

employer

to alter

how

ithandles allhiring

and

firingdecisions.

Unfortunately,

no comprehensive

dataexist onthe

number

or

outcome of

wrongful-discharge cases

under

these three doctrines.

Two

findings intheliteraturesuggest,

however,

thattheimplied-contract

exception

may

havealteredemployers' hiring practices (leaving asidetemporarilythe Dertouzos

and

Karoly

analysis, to

which

we

returnbelow). First,Miles (2000)

and

Autor

(2003)findthatemployers

substantiallyincreasedtheiruse

of temporary

help

agency

workersshortlyafter theirstatesadopted

implied-contract exceptions.Second,

Kugler

and

SaintPaul(forthcoming)findthatthe hiringodds of

unemployed

workers declinedaftercourtsintheir statesrecognizedtheimplied-contract exception.

Though

neither

of

theseresultsspeakstothecoreof ouranalysis

-

theimpact

of

these doctrines

on

employment

and

wages

levels

-

they

do

indicatethat

employers

were aware

oftheimplied-contractexception(ata

minimum)

and

took stepstomitigatelitigationrisks. 13

Itremainsacomplexlegalquestion,however,whether anemployerthatonceissuedahandbookorotherpromise of

jobsecuritycanmodifyittocreateat-willemployment. Several courtshaveheldthatsuchunilateralchangesbythe

employerarenotbindingonincumbentemployeesthathave previously received promises of jobsecurity.

Nor

wouldthiscaseloaddataprovideacompletemeasureoftheeconomiccosts of wrongful-discharge lawssince

theobserved caseloadisanequilibriumfunctionofemployerdecisionstoavertorsettlesuits(supply)andemployee

incentivestofilesuits(demand).

We

attemptedtotestwhether adoption ofawrongful-discharge exceptionbyastateincreased thenumberoflaw

B.

Hypothesized

effects

on

the

labor

market

As

discussed

by

Lazear (1991)

and

Blanchard and

Katz

(1997), thetheoretical impact offiring

restrictions

on

employment

levelsis

ambiguous.

Ina frictionless labormarket withcostless courts,the

Coase theorem

applies. Impositionof employer-sidefiringcosts arefully

undone by

efficientworker-firm

bargains, suchas the posting

by

workers

of

a

bond

equal to firing costs.

Where

the

Coasean

resultdoesnot

hold,firingrestrictionsreduceemployers' incentivesboth to hire

new

workers

and

fire

incumbent

workers

(Donohue,

1989). Accordingly,firingrestrictions

dampen employment

fluctuations,

which

may

raiseor

lower

employment

levels intheshortterm.

Over

thelonger term,if

employment

protectionraises

employment

costswithoutyielding correspondingproductivity increases,

employment

levelsand/or

wages

arelikely to fall. Thisisparticularlytrueifwrongful-dischargelaws encouragerent-seekingbehavior

by

employees

orinduce employersto retainunproductive workers

due

to fearoflitigation.

Not

all (non-Coasean)

employment

protectionadverselyimpactslabor

market

efficiency,however.

Employment

protectioncan beusefully

viewed

asa

mandated

employment

benefitthat,while costlyfor

employerstoprovide,isalsovalued

by

employees (Summers,

1989).

By

raising

employer

costs,

mandated

employment

protectionshiftslabor

demand

inward.

But

tothedegree that

workers

valuethe

mandated

benefit,laborsupply simultaneouslyshiftsoutward,

muting

theadverse

employment

impact. If

employees

valuethe benefitatitsfullmarginalcost,

wages

will intheoryfall tocoverthe costof providing the benefit

and

employment

levels will beunaffected(see, forexample, Gruber, 1994).

While

the overallimpact oferosionsoftheat-willdoctrine

on

employment

or

unemployment

isnot

clear apriori,existingevidence suggeststhattheimpact

may

differfor differentgroupsof workers. Several

Because

much

ofthese datahadtobe hand-coded,

we

wereonly abletoobtain dataonthreeyears(1979, 1985,and

1992-93).

We

foundthattheadoptionofthegood-faithexceptionbyCaliforniaandMontana,generallyregardedas thetwostatesmostaggressivelyerodingemploymentatwillduringthisperiod, significantly increased the shareof

employmentspecialtiesinthosestatesrelative tobothallpracticesandtotaxspecialities. Perhaps because ofthe crudityofthemeasuresandthefewyears,

we

wereunabletodetectconsistent patternsinotherstatesorforthetortor implied-contract exceptions. Detailsandtables areavailablefromtheauthorsuponrequest.

Moreover,asseveralauthorshaveargued, thepresenceof adverseselection inthelabormarket

may

cause

employerstoprovideinefficientlylowlevels ofjobsecurity(Aghionand Hermalin, 1990; Levine, 1991).Imposition

offiringrestrictionscouldthereforeraiseemploymentwhilereducing wages. Thiswouldcorrespondto acasewhere

authorsfind thatthe

employment

of younger, less-educated

workers

appears

most

likely tobe

harmed

by

wrongful-dischargeprotections, whileolderand

more-educated

workers appeartobenefit

(OECD,

1999,

Chapter2; Jolls,2000; Bertola,

Blau

and

Kahn,

2002).

We

examine

these disparateimpactsindepth

below

and

findimportant differences

by demographic group which depend on

thetime horizon examined.

II.

Data

sources

and model

specification

A.

Data

sources

To

measure

employment

andearnings,

we

draw on

thecomplete

CPS

monthly

filesfortheyears 1978

to 1999.

These

files provideindividual labor-forcedata forapproximately 100,000adultspersurvey

month

and

alsocontain

wage

data forone-quarterofthe

employed

sub-sample beginningin 1979.

'5

We

calculate

the

employment

topopulationratio (oritslog)and

median

loghourlyorfull-time

weekly

wages

of

currently

employed

workers foreight

demographic

groupsineachstateand timeperiod:

two

genders,

two

education groups (highschoolorless,

some

college ormore), and

two

age groups(18

-

39,

40

-

64).

16

To

maximize

usable variationinthetimingofthe adoptionof wrongful- dischargelaws,

we

code

the

legal

and

employment

variables at

monthly

frequency, as

was

done

by

Morriss(1995).

Hence,

if

two

states

adopta wrongful-dischargedoctrine 11

months

apartwithinthe

same

calendaryear,ourestimates

accurately accountfor thissubstantial differenceintiming.

Because

the

outcome

data areobservedathigh

frequency, serial correlationis a

major

concern.Followingthe

recommendations

ofBertrand,

Duflo

and

Mullainathan(2002),

we

apply

Huber-White

robust standarderrorsclustered

by

statethroughout.17

These

allowfor arbitrary errorcorrelations

among

observationswithin states, bothover time

and

among

demographic

groups.

For

ourlegalvariables,

we

developeda

taxonomy

of wrongful-discharge lawprevailingineachstate

Individuals

may

appearuptofourtimesinone calendar yearintheemploymentsample(notthe

wage

sample),

thoughtheirlabor forcestatus

may

differoneachoccasion.

Our

estimationproceduretakesaccountofpotentialserial

correlation

among

observations withineachstatesample.

Becausethewage sampleislessthanonequarter thesizeoftheemploymentsample,

we

usemedian wagesto

reducetheinfluenceofoutliers.Resultsusing

mean

wagesinsteadare,however,quitesimilar.

Except inTable4, inwhich

we

provide disaggregatedestimatesbyadoptercohorts,inwhichcasethere are

relativelyfewstateclusters.Here,

we

cluster thestandard errorsbystatefor contiguous time periodsbutassume

and

month-

yearforthetwo-decadeperiod

from

1978to 1999.

As

Morriss (1995)discusses, itisnot always

easytodate

when

astatehasadopteda particularat-will exception.

Our

objective is easily stated,however.

We

envision

management-side

employment

lawyers readingthe

advance

sheets andwritingawareness

lettersto their clients

when

major

changes occurinthe

common

law. Thus,

we

are interested inthefirst

courtdecisionin astatethat

would

triggeraclientletter

warning

abouta

law

change. Inpractice, our

independentassessmentofthelegal doctrinesin this areaforthe

50

states largelyagreeswith Morriss's list

of

relevantcases,although

we

had

toupdatethelistthroughthe 1990s.

18

InSection

V,

we

testthe

sensitivityof our conclusions

by employing

classificationsdeveloped

by

Dertouzos

and Karoly

(1992),

Morriss(1995), and

Walsh

and Schwarz

(1996)

-

thelastused

by

Miles(2000).

B.

Model

specification

Because

the

common-law

wrongful-dischargedoctrines

were

adopted indifferent

months and

years

by

most

U.S.states duringthe

1980s

and

1990s,

we

have

potentially

many

'experiments'to exploit.

Our

empirical approachistocontrastthe

change

in

employment

and

wages

of

demographic

subgroups within

statesadoptingagiven wrongful- dischargedoctrineina given periodto statesnotadopting

any

doctrine

duringthe

same

timeperiod.

To

implement

thisdifference-in-difference design,

we

needtoselecta'before'

and

'after'period for

pre-postcomparisons.

Although

we

could usetheentire 1978

-

1999

panel tocalculatethese contrasts for

eachstate,thisapproach has

two

disadvantages.First, becausestatesadopted exceptionsasearlyas

1979

and

as lateas 1998, thelong panel approachimpliesthatfor

some

states,observations

from

19yearsbefore

orafteradoption

would

be usedto

form

apre/postcontrast.Thisisunappealing. Second,thelong panel

approachexacerbates the serialcorrelation issuenoted above.

To

mitigate these issues,

we

primarilyusea

five-year pre-post

window.

The

24

calendar

months

priortoadoption

of

a doctrine aredesignatedasthe

pre-period;

months

13 to

36

following adoptionare designatedas the post-period;

and

thefirst 12

months

immediately following adoptionare excluded

from

thesample,toallowforan adjustmentinterval.

We

Although

we

usethe three-partdivisionoftheat-willexceptionsinthebodyof ouranalysis,

we

exploredthe

explore thesensitivity of ourresults to this setof choices below.

To

form

acontrol

sample

of non-adoptingstates,

we

include the

maximal

setof state-month

observationsforcorresponding calendar

months

(roundedtothenearestcalendaryear) for states thatdidnot

adopt

any

ofthe three doctrines duringthe relevant pre/post treatmenttime interval.

Note

that thisdesign

implies

some

statesserve as treatmentstates in

one

period

and

controlstates inanother, althoughnever

within a five-year

window

surroundingtreatment.

The

basiceconometric

model

that

we

estimateis

(1)

Y

_a

=a

+

P,

L

s

+

P

2Post„

+

y

Postsl -Ls

+

es,,

where

Y

sl is

employment

or earnings fora

demographic

groupin state 5

and

timeperiod t,

L

t

isa

time-invariant

dummy

variableequal tooneifa statewill adopta given exceptionduringthe pre/post

sample

interval

and

Post_a is a

dummy

variableequal to

one

in

months

13 to36 followingadoption.

The

coefficientofinterest, _y,is anestimate

of

thepre-post

change

inthe

outcome

variableinadoptingstates

relativeto thecorresponding

change

innon-adoptingstates. All estimates are

weighted by

the

sum

of sample weightsin the state-year-month-demographiccell,reflectingtheestimatedcountof U.S. residentsor

employed

personsinthecell for

employment

and

earningsrespectively.

We

enrichthisbasic

model

inthree ways.First,inplaceofthe

common

main

effect

and

pre-treatment

indicators

(a and

L

s),

we

add

main

effectsforeachstate

and

their interactionswithatreatment indicator variable. Second,tonon-parametricallyaccountfor

common

national shocksto

employment

overall

and

by demographic

group,

we

also include

dummy

variablesforeach

monthly

calendartimeperiod interacted

withindicatorvariables foreachoftheeight

demographic

groupsin thesample.20Finally,to accountfor

common

regionalshocksto

employment,

we

alsoestimate

models

thatinclude interactions

between

calendar-year

dummies

and

indicator variablesdenotingthenine

Census

geographic regions.

With

these

relevant or empirically robust. Supplementaltables are availablefromtheauthorsonrequest.

Ifa stateservesinboththecontrolandtreatmentgroupsin agiven model,

we

alsoincludea statextreatment

dummy

equaltooneinthe24monthsimmediately precedingtreatment.

regioncontrols included, the parameter

y

isidentified only

by

the

contemporaneous

contrastin

employment

or

wage

outcomes

in adoptingversusnon-adoptingstates located inthe

same

geographic

regions.

III.

Impacts

on

employment and

earnings

Beforeestimatingequation(1),

we

providea visual

summary

of

thedatainFigures 1 through6.

These

depictestimatedlog

employment

topopulationrates(Figures 1

-

3)andlog

median

wage

levels(Figures

4

-

6)in adoptingrelative tonon-adoptingstatesat

monthly

intervals inthe

48

months

priorthrough

96

months

following adoptionof eachdoctrine.

Wage

and

employment

levels inthefirstfull

month

following

adoptionare normalizedatzero. 21

The

dashed

lines ineach figurerepresentrobust

90

percentconfidence

intervaIsforeach

monthly

point estimate.

These

figuresprovideinitial evidencethat

one

wrongful-dischargedoctrine, theimplied-contract

exception,didindeed affect state

employment

levels.

As

isvisible inFigure 1,relative(log)

employment

to

populationratesforbothmales

and

femalesdip

by

approximately 1.5to2percentoverthe2years

following adoption

of

theimplied-contractexception,reaching anadirafterapproximately

30

months.

By

contrast,Figures2

and

3providelittleevidencethatthe public -policy or good-faithexceptionsaffected

employment.

One

cannot

make

stronginferences

from

thesefigures,however.

As

isvisible

from

the

wide

standard-errorbands, the

monthly

point estimates arerelativelynoisy. Inaddition,these

models do

not

inchde

thefullsetofcontrolsthat

we

(later)useforestimatingequation (1).Nevertheless, theformal

analysis

of

employment

below

largelybearsout theimpression given

by

thefigures.

Figures4 through 6repeatthisexercise for

median

log

weekly

earningsoffull-timeworkers.

Because

21

Thesefiguresplotthe coefficientand90percentconfidencebands fromestimatesof parameters _y

r from the followingequation: 96 r=-48 where,asabove, Y

s:j,istheoutcomevariable foragivendemographicgroup,state,and timeperiod,

5

,<p

l

and

n

.

are vectorsofstate,time,anddemographic groupmaineffects,and L

sl is

a

dummy

variablethatassumesthevalueof

one(only)inthemonththat a stateadoptsagivendoctrine(theimpactof eachdoctrineisestimatedsimultaneously).

thesamplesusedforthese estimates arelessthan

one

-fourth as large as the

employment

estimates,thereisa

great deal

more

variability in these observations.

These

figuresprovidelittle

prima

facie evidencethat

wrongful-discharge doctrines affected

wage

levelsof

employed

workers.

A. Initialestimates:

Employment

and

Wages

Table 1 presents estimatesof equation (1)for

employment

and

wages.

What

emerges

clearly

from

the

estimatesin thistable isthatadoption oftheimplied-contractexceptionisassociatedwitha

modest

but

meaningfulreductionin

employment.

In

column

1 of Panel A,

we

estimatethat adoption ofthe

implied-contract doctrinereducesoverall

employment

topopulation

by

2.0percentinthesecond

and

thirdyears

following adoption (t

=

4.1).

When

controls are

added

tothe

model

toabsorb region-by-year

employment

shocks

(column

2),thepointestimate

and

itsstandarderrorare bothreduced

by

approximatelyhalf,

indicatingthattheimplied-contract doctrine

was

typicallyadopted

when

employment

conditions

were

at

slightlyabove-averagelevels (a factalsosuggestedinFigure 1).

The employment

impactis estimatedat

-1.0percentagepoints,

which

ishighly significant(t

=

3.2).

The

next

two rows

ofthetablerepeat these estimatesforthepublic -policy

and

good-faith doctrines.

The

public-policy doctrine isassociatedwitha smallreductionin

employment,

butthese reductions are

neversignificant.

The

point estimates forthegood-faithdoctrine areof approximatelyequal

magnitude

to

thoseforthe implied-contract association.

These

coefficientsaremarginallysignificant

and

arenot typically

robusttoinclusion ofregion-by-yearcontrols. Sincetherearefewergood-faithadoptions than forother

doctrines (13 forgood-faithversus43

and 34

forimplied-contractandpublic-policy),there

may

be

inadequatestatistical

power

toreliablydetectitsimpacts.

As

one

specificationcheck,

columns

3

and

4 of Table 1 replace the logemployment-to-populationratio

measure

withitslevel.

The

outcome

variableis

now

thepercentagepoint

change

in

employment

to

employment

topopulationareveryslightly smaller, whilestatisticalsignificanceisunaffected.22

Panel

B

of Table 1 presents

comparable

estimatesforboth

median

loghourly andfull-time

weekly

wages. In

no

case arethepoint estimates statisticallysignificant.

However,

a notable patternisthat

doctrinesthatappeartoreduce

employment

(implied-contractand,toa lesserdegree, good-faith) are

associatedwitha

modest

increasein

median wages

of

employed

workers.

One

explanationforthispattern

isthat

workers

whose employment

isreduced

by

adoption

of

a wrongful-discharge

law

are typically

below

the

median

earnersin their state

-demographic

cell.

Hence,

their

removal

from

theobservedearnings

sample

raisesthe

median

wage

slightly.

We

provide furtherevidence

on

therelevance ofthisexplanationbelow.

B.

Does

the specificdoctrine

matter?

Given

the generallynegative estimated

employment

impact

of

each category ofdoctrine,

one

potential

interpretationoftheseresults isthatitisnotthespecificdoctrinethatmattersbutsimplythefact that

any

wrongful-dischargedoctrinehas

been

adopted.

To

examine

thisissue,

we

estimateinTable 2 aset

of

models

that

compare

theimpactsof an 'anydoctrine' variableagainstadisaggregatedsetofthreedoctrine

variables.

As

withtheprevious models,

we

specify the two-year periodpriortolaw

change

as the

pre-treatmentperiod

and

thetwo-year period

commencing

one

yearafter

law change

asthepost-treatment

period.23

The

first

two columns of

Table 2 confirmthat,

on

average,adopting

any

doctrineappearstolower

employment by

between

0.5

and

1.0percent, withthesmaller point estimatecorrespondingtothe

model

in

which

region

by

timeeffectsare controlled. In additiontothe any-doctrine

dummy,

Columns

3

and

4

add

22

We

alsoestimatedTable1 without usingthe

CPS

sampling weights,whichyieldedcomparableresults,as

shown

in

AppendixTable2.

By

comparisonwiththeweightedestimates,thistableshows: 1)thepointestimatesforthe Implied-contractexceptionareabout2/3rdsas largeinabsolutemagnitudeforemploymentandstillhighly significant; 2)thePublic -policyand Good-faith exceptionsarealsonegativeand marginallybut not robustly significant; 3)the

wage

estimates aresimilar;and4) theR-squaredsare lower, consistentwiththeinefficiencyofthe

weighting(orlackthereof).

23

An

additionalwrinkleinthisspecificationisthatseveralstatesadoptmultiple doctrines withina fiveyear

window

and hencethepre-andpost-periodsarenot unique.In estimating thesemodels,

we

includeallrelevantpre-and

post-treatment observationsforagivenstate- meaningthatsometreatmentandcontrolperiodsoverlap -andinclude,as in

equation(1),treatmentand treatmentx post effectsforeach doctrine.Controlobservations are selected identically to

anindicatorvariableforeach ofthe threedoctrines.Notably,the any-doctrine

dummy

ispositiveinthese

specificationswhile each

of

the three individual doctrine

dummies

isnegative and, in

most

cases,

significant.Thissuggeststhatitis notsimply thepresence

of any

doctrinethatreduces

employment

levels;

thespecificdoctrinedoesmatter.

Because

the neteffectofa doctrinein

columns

3

and

4isthe

sum

ofitsindividual

dummy

and

the

any-doctrine

dummy,

itis useful toeliminate theany-doctrine

dummy

toget a clearerpicture. Thisis

done

in

columns

5 and6.

When

theimpactofalldoctrines isestimatedjointly,theimplied-contractdoctrine

remainsrobustly negative

and

similarin

magnitude

tothe Table 1 estimates.

The

good-faith doctrine again

proves non-robusttoinclusion

of

region-by-yearcontrols.

Panel

B

of

thetableperformsthe

same

exercisefor

wage

outcomes.

As

above, the any-doctrine

dummy

doesnot survive inclusionofindividual doctrine controls.

The

dataagain provide

modest

evidence of a

positive

wage

impact

of

theimplied-contract and,

more

sizably, thegood-faith doctrine.

C.

Checking

for

composition

bias in the

wage

estimates

Estimates

of

theimpactof wrongful-dischargelaws

on wages

may

suffer

from

composition bias: since

wages

areonlyobservedforcurrently

employed

workers, wrongful-discharge lawswill raiseobserved

wages

iftheydifferentiallyreduce

employment

of

low -wage

workers.

One

means

totesttherelevance

of

thisexplanationis toadjust

wage

observations for sele ctivewithdrawal.

We

do

this following

Chandra

(2002)

by

estimating

median

wages

within state-year-month-demographiccellsacross allpotentialworkers

-

employed

and

non-employed

-

and

assigning a

wage

of

zeroto

non-employed.

This 'inclusivemedian'

approachstands incontrasttothe standard 'exclusivemedian' calculationsused above,

which

removed

non-employed from

the samples.

Because

theinclusive

median

implicitly

assumes

that

non-employed

workers

would

earn

below

the

median

wage

intheirrespective state-time-demographic

group

cell, itplaces

theestimated

median

lowerinthedistributionofcellwages.

One

shortcoming withthisapproachisthatif

50-pluspercentofpotentialworkers ina cellare non-employed,the

median

cell

wage

will be zero and

hence

thecell

must

bediscarded,

which

excludes

most

femalecellsas well ascellswith highparticipation

same

cellexclusionstoboththe exclusive

and

inclusivemedians.

Panel

A

of Table3 presents difference-in-difference

wage

estimatesforconventionalexclusivehourly

wage

medians

akintoTables 1 and2.

These

estimates

echo

theearlierfindingthatobserved

wages

rise

significantlyafteradoptionofawrongful- dischargedoctrine,particularlythe implied-contractexception

(see

column

6). Panel

B

presents

comparable

models

forthe inclusivemedians.

These

estimates effectively

reverse the positive

wage

finding. In

many

cases,the point estimatesfortheimpactof adoption

of

a

wrongful-discharge

law on wages

are

now

negative. In

no

caseare theestimates significantlypositive.

Thisset

of

resultssuggeststhat

employment

declines associatedwith adoptionof a wrongful-discharge

law

couldpotentially generatesignificant

upward

compositionbiasin observed wages.

Given

thesensitivity

ofthe

wage

estimatestocomposition bias,

we

focustheremainder ofthe analysis

on

employment.

D.

Cohort

effectsin

adoption?

The

precedingestimatespool all yearsofdatatoincrease the precisionofthe estimates.

The

cost

of

this

approachis thatit

masks

any

temporalheterogeneityinthe

economic

impactofthe doctrines. Table4

studiesthispotentialheterogeneity

by

tabulating theeffectof each exception

on

employment

and

earnings

forthefollowing adoption 'cohorts':

1980

to 1983,

1984

to 1987, 1988to 1992,

and

1993to 1998.24

The

15statesthatadoptedtheimplied-contractexception during

1980

to 1983 experienceda declineof

-0.5to-1.9percentin

employment

during

months

13 through

36

following adoption(thesmaller estimate

correspondingtothe

model

with region

by

yearcontrols).

The

18 statesthatadoptedthisexception

between

1984

and

1987also experiencedsimilarly large

employment

declines.

By

contrast,

we

do

notfindrobust

evidencethatthefinalset

of

10statesthatadoptedthedoctrine

between

1988

and

1992 experienced

any

negativeeffect

on employment,

althoughthe directionisgenerally negative.

The

nextfour

columns

of Table 4repeatthese estimatesfor statesadoptingthepublic -policy

and

good-faithexceptions.

These

estimates giverisetowidely varyingsignsand magnitudesforeachdoctrine

and

Adoptioncohortdates refertotheyearawrongful-dischargedoctrineisenacted; the pre-andpost-periodsusedto

formtheemploymentcontrast are aswithpriorestimates thesurroundingfiveyears (2 priortoadoption,3post adoption,withthefirstomitted).

We

donotstudy adoptionspriorto 1980toallowforthetwoyearpre-treatment period.

No

implied-contract or public-policyexceptionswereadoptedafter1992.

time period,andare quitesensitive totheinclusion ofregion

by

yearcontrols.Thissetoffindingsreduces

our confidencethatthe good-faithexception adversely affected

employment

levels,exceptperhapsforthe

initialcohortof adoptingstatesin theearly 1980s.

An

interestingpattern that

emerges

from

Table

4

is thattheimplied-contract

and

good-faith doctrines

appearto

have

had

smaller(orzero)

employment

impacts

among

lateradoptingstates.

One

explanationfor

thispatternis thatearlyadoptingstates

may

have been

thosethat

were most

aggressiveintheirpursuitof

employee

rights

and

thusexperiencedgreaternegativeeffects on

employment.

Another

explanation isthat

employersinlateradoptingstatesanticipatedthe eventualadoption ofthe doctrines

and

hence largely

responded in advance, therebycausingtheregression estimatesforthelateadoptionstounderstate thetotal

effect.

A

thirdpossibilityisthatthestate level impact ofthe

law

differs

when

few

states

have

previously

adoptedtheexception than

when

most

states

have

already

done

so.

Employment

declines foundfor early

adopters

may

partly reflect decisions

by employers

tolocateinotherstates,apossibility thatislargely

foreclosed

when

most

states

have

alreadyadoptedanexception.

The

diminishingeffectsalsosuggesta

fourthexplanationoffered

by Edelman,

Abraham

and

Erlanger(1992).

These

authors arguethat

professional(non-academic)

law

journals

and

personneljournals overstated thethreat

posed

by

the

implied-contract doctrine,leadingtoexcessive

management

changes. Benefiting

from

the experienceofthese early

adopters,

employers

in lateradopting states

might have

reactedlessseverelytoadoptionof

wrongful-discharge doctrines.25

E.

Longer

term

impacts

and

alternative

timing assumptions

Inourbaselinespecification,

we

usethe

24 months

priortoadoptio

n

as ourpre-treatmentperiodandthe

months

13 to

36

following adoptionasthepost-treatment period. InTable5,

we

measure

longerterm

impacts

of

thewrongful-dischargedoctrines

and

additionally explore thesensitivity

of

ourfindingsto

alternative choices

of

pre-andpost periods.

For example, Business

Week

inJuly 1985ranaratheralarming coverarticleon"TheRevolutioninEmployee

Rights"that stated,"To minimizeliability,corporationshaveto treateachdismissalasthoughitwereundera 'just

The

first

column

of Table5 repeatsourbaseline specification for

employment from

Table 1.

Columns

2

through 6 ofthetable

move

thepost-adoptiontreatment

window

closertothepointof adoption

by

1 year

(i.e.,immediatelythereafter)

and

then

outward

by

1,2, 4,and 6 yearsrespectively.In thefinal column,

column

6,the post-treatmentperiodisyears7

and

8 followingadoption.

These

estimates indicatethatthe

employment

effectofthe implied-contract doctrinereaches a

maximum

inthe

two

yearsfollowing

adoption,

and

thisimpact appearstograduallydiminishthereafter.

By

years7

and

8,the estimated

employment

reduction isconsiderably smaller thanthe baseline

and

isinsignificant (apattern also

suggested

by

Figure 1).

By

contrast,theestimated negativeeffect

of

thegood-faith doctrine increaseswith

time,butthiseffectisneversignificant.

To

testthesensitivity oftheresultstothe selectionofthe /?re-rreatmentperiod,

columns

7

and

8 ofthe

table adjustthe pre-treatmentinterval

outward

by

1

and

2 years respectively (using the baseline

post-treatmentperiod ofyears 1

and

2 followingadoption).

Column

7

compares

employment

in years 2

and

3

priortoadoptionto

employment

inyears 1

and

2 followingadoption,

and

column

8 performsthis

comparison

foryears4

and

3 priortoadoption.

Changing

thepre-treatment

window

doesnot greatlyaffect

the patternofresultsbutdoes reduce the precisionofthe estimates.

When

region

by

year

dummies

are

included, the implied-contract doctrine

no

longer has asignificant

employment

effect.

IV.

Are

all

workers

equally

affected?

Liketheir

European

counterparts,U.S. wrongful- dischargelawsdisproportionately protect

workers

with longer tenure andhigherwages.Long-tenureworkers are typicallyableto

make

a

prima

faciecasethat

theirjobs provided anexpectation

of

ongoing

employment

(inthecase ofthe implied-contractdoctrine),or

anexpectation offuturebenefitsforcurrent service (good-faithdoctrine). In addition, court

awards

tendto

be roughly proportional topriorearnings

-

particularly in implied-contractcases

-

and hence high

wage

workers havea greaterincentivetolitigate.

26

Sincetheprotectionsoffered

by

wrongful- discharge doctrines

Thisisparticularlytruebecauseattorneys' fees are usuallyarrangedonacontingencybasis;theattorney receivesa

percentage oftheaward ifthecaseissuccessfulandtypicallyno paymentotherwise. Consistentwiththesefacts,

are notequally distributed

among

worker

groups, it isuseful toask

whether

the

employment

impactsalso

differ

among

demographic

subgroups.

We

explorethispossibility inTable 6

by examining

the relationship

between

theadoptionof

wrongful-discharge lawsandthe

employment

rate

of

each ofthe 8

demographic

groupsthat

were

pooled inthe

above

analysis. Consistentwiththeabove,theresults inTable 6 confirmthatthe implied-contract doctrine lowers

employment

rates across the board.

But

thesizeofthe impactdifferssubstantially

by demographic

group.

The

largestimpacts areuniformly

found

forfemale, less-educated (high school orless), and

younger

(under

age 40) workers.

These

impactsare intherange of -1.0to-2.7 percentage points.

Young,

less-educated

femalesfare worstofall.Notably,the

one demographic group

for

whom

thereis

no

evidenceof an

employment

impact(for eithergender) isolder,more-educated workers.

We

also findmodestlyrobust

evidence(largepoint estimates, large standarderrors)

of

anegativeimpact

of

thegood-faithexception

on

employment

rates.

But

this impactisonlydetected for

women

and younger,less-educated

men.

As

agroup,theTable6 resultsappearconsistentwitha

number

of

OECD

studiesthatfindthat

employment

protectionstendto differentially

harm

employment

offemales, less-experiencedworkers

and

less-skilledworkers(Bertola,

Blau

and

Khan,

2002;

OECD,

1999). Yet, intheU.S.context, theseresults

appear

something

ofa puzzle.U.S.wrongful-dischargedoctrinesincrease the expectedcostof

employing

high-tenure, high-

wage

workers.

These

highercosts shouldlowerthe

employment

and

earnings

of

these

groups

and

raise

demand

for

workers

who

areclosesubstitutes

-

low-wage and

short-tenure

employees

who

areunlikelyto(successfully)litigate.

27

Yet,thisisoppositeto

what

we

find.

Why

do

wrongful-discharge laws

harm

the

employment

rates oflessprotectedworkers?

Two

rationales arefoundin theliterature.

One

isthat less protectedgroups

-

females, less-educated,

and

younger

workers

-

have greateropportunitycostsof

work

(i.e.,better opportunities in

home

production,

school enrollment,

and

leisure)

and

accordinglytheirlaborsupply isrelatively elastic. If

employment

hold executiveormanagerialpositions (53 percent),have 6ormoreyearsoftenure (48 percent),and

eam

considerablyabovethemedianwage.

This

may

indeed bewhatoccurredwiththesurgein

demand

fortemporary helpemploymentafteradoption of

protection ischosen to

maximize worker

welfare,itwill optimally price

many

oftheseworkersoutofthe

labormarket,raisingtheir

wages

and

reducingtheir

employment

(Bertola,

Blau

and

Khan,

2002).

An

alternative explanation offered

by Lindbeck and

Snower

(1988)

and

SaintPaul (2002)isthat

employment

protection istypicallyadopted toprotect

incumbent

('insider') workers

who, on

average,are likely tobe

older,more-skilled males.

These

protectionsreduceproductivity

and

generate rents forincumbents,while

weakening

earnings

and

employment

prospectsforyounger, less-skilled,

and

lessattached labor force

participants('outsiders').

Both

theoriestherefore offerarationale for

why

women,

younger and

less-skilled

workers

are

harmed

by

employment

protection.

Do

theyfittheU.S. facts?

Incase ofthe firsttheory,the intervening

mechanism

by which

employment

protectionlowers

employment

of

'more

elastic' workersis

by

raising their relativewages. Thispredictiondoesnot

seem

tofit

theU.S. case. Inparticular,itisunclear

howU.S.

wrongful-discharge laws coulddisproportionatelyraise

employment

costs forthe'elastic' groupssincetheseworkersareprovidedrelatively less

employment

protection.

And

while ourdata offer

some weak

evidencethatthe

wages

ofelasticgroups

do

increaseafter

adoption

of

wrongful-dischargedoctrines,

we

view

thisevidenceasprimarily driven

by

selectionof

low-wage

workersinto

non-employment. Hence,

inour view,thefirstexplanationdoesnotappearviable.

The

second, 'insider-outsider' explanationis

more

promising. Ifwrongful-dischargelawssuccessfully

deter

employers

from

terminatinghigher

wage

and

longertenure

workers

('insiders')

and

further

employers

arenot abletoreducethe

wages of

protectedgroupsinthe short run,employerswill

presumably

need

to

reducehiring of

some

worker

groupstomaintain

employment

levels. Inthiscase, wrongful-discharge laws

willprotect thejobs of

more

seniorworkersbut the costwillbe borne

by younger

workers

who

arenot

hiredin theirplace.Thisisroughlythe

mechanism

posited

by

the insider/outsidermodels.

Over

the longer term,however, employers shouldprefertoreduce

employment

ofseniorworkers

relative to lessexpensivealternatives.

Although

this longer run

outcome

is

presumably

difficultto

measure

More

generally,ifadoptionof wrongful-discharge laws inducesanygeneralemployerreluctanceto hire

new

workers,thisimpactwillfirstbevisible in adeclineintheemploymentratesof high turnoverworkergroups

inaggregate data,

we

make

apreliminaryeffortinTable7. Here,

we

estimatelong-run

difference-in-difference

models

for state level

employment

by demographic group where

we

contrast the

change

in

employment

in adoptingversusnon-adoptingstates in years fiveandsix following

law

adoptionrelative to

years

two

and onepriortoadoption.

As

would

be expected, the point estimatesin thistable arenot

precisely estimated.Nevertheless, anoteworthypatternisthattheestimated long-run negativeeffectsofthe

implied-contract doctrine

on

the

employment

ofolder

and more-educated

workersaregenerally larger than

thosefor younger,less-educated

worker

(andin

many

cases, largerthantheshort-runestimates

from

Table

6). Similarly,thelong-run estimatesfor

younger

and

less-educatedworkersaregenerally substantially

smallerthan the shortrunestimates,

and

in

some

cases

weakly

positive. 30

Innet,ourestimatesconfirmpatterns

from

the

OECD

that

employment

protection

does

reduce

employment

oflessprotected

worker

groups

-

females,

and younger and

less-educated individuals

-

atleast

inthe shortrun.

While

less decisive, ourlongerterm evidence suggeststhatthe

harms

interms

of

reduced

employment

tendtoaccruetothe

workers

whose

expected

employment

costs are raised

by

thesedoctrines.

Thisresult

may

suggestan importantdifference

between

employment

protectionsprovidedinthe

OECD

and

UnitedStates.

Whereas

OECD

employment

protections typically bar terminationsofseniorworkers

exceptunder very limitedcircumstances,thewrongful-dischargedoctrinesrecognizedintheUnited States

provide

no

such formal

employment

security.Rather, they

make

itfeasible for certainworkerstolitigate

afterterminationatconsiderable

monetary

and psychiccost,

and

withlimited certaintyofredress.

By

raisingexpected

employment

costsofseniorworkers without providing

them

formaljobsecurity,U.S.

wrongful-discharge laws

may

make

it

more

likelythat

employment

of

protectedgroups isultimately

reduced.

disproportionate shareoftheunemployed,thisexplanationisconsistentwithKuglerandSaintPaul's(forthcoming)

findingthat exit ratesfrom unemploymentslowafterstatesadoptedimplied-contract doctrines.

Hence,these specificationsareidenticaltocolumn 5of Table5but areestimatedseparatelybydemographicgroup.

Estimatesusing an alternativelong-runpost-periodofyears7and 8following adoptionproducedqualitatively similar

resultsandareavailableonrequest.

The

exceptiontotheclaims ofthelasttwosentencesiscausedbythe relatively largenegative(albeit statistically

insignificant) long-termeffectfromthe implied-contractexceptionforyoung, low-education males(column 2of Table

V.

Reconciling

with previous

studies

Our

findingthatunjust-dismissal laws

-

theimplied-contractexception in particular

-

have

had

a

modest

buteconomicallymeaningful adverse impact

on

state

employment

ratesstands incontrastto

two

publishedpapers exploringthe

same

questions.

The

first,awidely citedstudy

by

Dertouzos

and Karoly

(1992

and

1993,

D&K

hereafter),

found

that states' adoption

of

exceptionsto

employment

atwill over

1980

to 1987 reduced aggregate state

employment

by 4

to5 percentagepoints,with

even

largerreductionsin

employment

inthe service

and

financialsectors.

The

magnitude

ofthese estimates,roughlythreeto five

timesas large asourestimates,garneredconsiderableattention in

academic

journals

and

policy debates.31

More

recently,

Thomas

Miles(2000),using a

methodology

more

comparabletoour

own,

found

no

effect

of

unjust-dismissal doctrines

on

aggregate

employment

or

unemployment.

To

understandthesourceofthe

discrepancies

between

these

two

studies

and

our

own

findings,

we

reanalyzed both papers.

A.

The

Dertouzos

and

Karoly study

Our

difference-in-difference

methodology

estimates theimpacts of wrongful-dischargedoctrines

by

contrasting

contemporaneous

employment

and

wage

changesinadoptingversusnon-adoptingstates.

D&K

eschew

this source ofvariation,arguingthatthe adoptionofstatelaws

may

bedriven

by

the 'supply

and

demand'

for legal doctrines.

To

correctfor this postulatedendogeneity,

D&K

employ

asetofinstrumental

variablestopredictstates' adoption

of

wrongful-dischargedoctrines

and

thenusethese predicted valuesin

place

of

the actual laws.

Specifically,

D&K

estimatean equationofthe

form

(2)

\n(emp

_a

)=a+Y-L

jl +<ps

+d,+e

st ,

where

In

emp

sl islog total

employment

in state s

and

year t,and

L

j: isthepredicted probabilityofthe presence

of

each doctrineinthestate

and

year.Thispredicted probability isestimated

from

a log

odds

regressionoftheobserved

law

variables,

L

Jt ,

on

asetofinstrumentalvariables,

Z

sl,

and

vector

of

year

Forexample, duringhisgubernatorial carrpaign, CaliforniaGovernorPeteWilsonprominentlycitedDertouzos and

dummies

S

I .

(3)

Pr[Z„=l]

=

Pr[Z;,/3

+

<5,

>-eJ.

The

instrumentsused

by

D&K

inestimatingequation (3) include

whether

a state

had

aRepublican

governor, thestate's level and change inunion

membership,

thestate's

change

inlawyers percapita,the

fractionof borderingstatesrecognizinga similardoctrine,and anindicatorfor

whether

astate

had

arightto

work

law

in 1980.

As

D&K's

estimates

of

equation(3) indicate, these latter

two

variables are indeed highly

correlatedwithstates' propensitytoadopt

common

law

exceptions.

A

potentialconfound,however, isthat

both

measures

are alsolikely tohaveadirectcorrelationwith

employment

levels thatdoes not

emanate

from

their influence

on law

adoption.

The

source of our concernisvisible in Figures7 and 8.

As

noted

by

Blanchard

and

Katz

(1992) and

depictedinFigure 7,

employment growth

inthe South has exceededthat inthe

non-South

forthe pastsix

decades.Thistrend substantiallypredates theadoptionofunjust dismissal laws

and

likelystems

from

factors including theadventofairconditioning(whichincreasedhabitability

and

manufacturing

productivity intheSouth,

most

notably intobaccoandprinting),and civil-rights-eralegislation that

increased

wages

and

employment

of Southernblacks (Arsenault, 1984;

Donohue

and

Heckman,

1991).32

Moreover, asis

shown

inFigure 8, Southern states

were

last

and

leastlikely to adopt wrongful-discharge

doctrines,

meaning

that theirfractionof borderingstatesadopting exceptions

was

also

much

lower.

Furthermore, 85percentof Southernstates

had

aright-to-

work

law

in 1980 versus only

25

percent

of

non-Southem

states.

33

Given

the positive correlation

between

Southernregion

and employment growth and

thenegative

correlation

between

Southernregion

and

adoptionof wrongful-dischargedoctrines,it isa near certainty that

Thereisnoformalagreement onwhichare theSouthernstates.

We

useAlabama,Arizona,Florida,Georgia,

Kentucky, Louisiana, Mississippi,

New

Mexico, Northand SouthCarolina,Tennessee, Texas,andVirginia.

Non-SouthernstatesincludeallotherU.S.statesexceptfor

DC

and,duetolackofemploymentdataextendingto1939,

Alaska, Hawaii,Illinois,Michigan,and Minnesota.GrowthratescalculatedinFigure7useeachstate'sshareofSouth