School Finance Reform and the Distribution of Student...
Transcript of School Finance Reform and the Distribution of Student...
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SchoolFinanceReformandtheDistributionofStudentAchievement*
July2016
JulienLafortune
UniversityofCalifornia,[email protected]
JesseRothstein
UniversityofCalifornia,BerkeleyandNBER
DianeWhitmoreSchanzenbachNorthwesternUniversity
ABSTRACT
Westudytheimpactofpost-1990schoolfinancereforms,duringtheso-called“adequacy”era,onabsoluteandrelativespendingandachievementinlow-incomeschooldistricts.Usinganeventstudyresearchdesignthatexploitstheapparentrandomnessofreformtiming,wefindthatreformsleadtosharp,immediate,andsustainedincreasesinspendinginlow-incomeschooldistricts.UsingrepresentativesamplesfromtheNationalAssessmentofEducationalProgress,wealsofindthatreformscauseincreasesintheachievementofstudentsinthesedistricts,phasingingraduallyovertheyearsfollowingthereform.Theimpliedeffectofschoolresourcesoneducationalachievementislarge.
*ThisresearchwassupportedbyfundingfromtheSpencerFoundationandtheWashingtonCenterforEquitableGrowth.WearegratefultoApurbaChakraborty,EloraDitton,andPatrickLapidforexcellentresearchassistance.WethankJulieCullen,TomDownes,KiraboJackson,RuckerJohnson,RichardRothstein,MaxSchanzenbach,andconferenceandseminarparticipantsatAPPAM,AEFP,Bocconi,Brookings,Chicago,Erasmus,Wisconsin(IRP),LSE,NewYorkUniversity,Northwestern,Princeton,RAND,Teachers’College,TexasA&M,Warwick,andthe2015Stavanger-Bergen-Berkeleyworkshopforhelpfulcommentsanddiscussions.
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Introduction
Economistshavelongbeenskepticalofresource-basededucationpolicies,
basedinpartonobservationalstudiesshowingsmallorzeroeffectsofadditional
funding(see,e.g.,Colemanetal.1966,Hanushek1986,Hanushek2006).2Hanushek,
forexample,writes:“Simplyprovidingmorefundingoradifferentdistributionof
fundingisunlikelytoimprovestudentachievement(eventhoughitmayaffectthe
taxburdensofschoolfinancingacrossthecitizensofastate)”(1997,p.153).
Accordingly,recentpolicydiscussionshavefocusedonwaystoimprovethe
productivityofexistinginputsratherthanonchangesinschoolresourcelevels.
Nevertheless,stateshavecontinuedtoimplementaggressiveresource-based
policies,aimedinpartatreducingachievementgaps.Between1990and2011,
averagerealspendingperpupilinK-12schoolsrosebyabout40%.Thisincrease
wasconcentratedinlow-incomeschooldistricts.Figure1showstheevolutionof
averagerevenuesperpupil,in2013dollars,inthelowest-incomeschooldistricts
(definedasthebottomfifthofeachstate’sdistrict-levelmeanhouseholdincome
distribution)andthehighest-incomedistricts(thetopfifth),from1990to2011.3
Overthisperiod,realper-pupilrevenuesrosebyroughly30%inthehighest-income
districts,andby50%inthelowest-incomedistricts.Thus,whilelow-income
2Therearealsoobservational(CardandKrueger1992a)andexperimental(Krueger1999;Dynarski,Hyman&Schanzenbach2013)studiespointingtopositiveschoolresourceeffects.Thereisnoconsensusabouthowtoreconcilethese(see,e.g.,Burtless1996;Hanushek2003;Krueger2003).3HawaiiandtheDistrictofColumbiaareexcluded.Statemeansweightdistrictsbylogenrollment,thenareaveragedwithoutweightsinFigure1.Numbersinthetextweightstatesbyenrollmentforcomparabilitywithnationalaggregates.WediscussdatasourcesanddefinitionsinSectionIII.
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districtscollectedabout15%lessthanhigh-incomedistrictsin1990,theyhave
beeninroughparitysincearound2001.
Muchofthischangecameviareformstostateeducationfundingformulas.
Figure2showsrevenuesoflow-incomedistrictsrelativetohigh-incomedistricts,
eachdefinedasinFigure1,separatelyforthe26statesthathaveimplemented
schoolfinancereforms—typicallybutnotalwaysundercourtorder—since1990
andfor23statesthathavenot.Growthinlow-incomedistricts’relativerevenues
hasbeenmorethantwiceasrapidintheformerstatesthaninthelatter.
Theimplicationsofschoolfinancereforms(SFRs)fortheleveland
distributionofschoolfundinghavebeenmuchstudied(see,e.g.,Hanushekand
Lindseth,2009;CardandPayne,2002;Murray,Evans,andSchwab,1998;Laddand
Fiske2015).Theexistingresearchfocusesprimarilyonso-called“equity”reformsin
the1970sand1980s,whichaimedtoreducedisparitiesinfundingacrossdistricts.
Butmostreformssince1990havebeen“adequacy”reformsthataimtoachievean
adequateleveloffundinginlow-incomedistricts,regardlessoftheimplicationsfor
equity.Adequacyreformshavebeenmuchmorenumerousthantheearlierequity
reforms,buthavebeenmuchlessstudied.
SFRsarearguablythemostsubstantialpolicyeffortaimedatpromoting
equalityofeducationalopportunitysincetheturnawayfromschooldesegregation
inthe1980s.Butthereislittleevidenceabouttheireffectsonstudentachievement.
Whatevidencethereisderivesfromnon-representativedataonstudentswhotook
theSATcollegeentranceexam(CardandPayne2002);fromlong-runoutcomes
measuredintherelativelysmallPanelStudyofIncomeDynamicssample(Jackson,
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Johnson,andPersico2016);orfromcasestudiesofindividualreforms(Clark2003;
Hyman2013;Guryan2001).4Thesestudiesprimarilyexaminepre-1990,equity-
basedSFRs,andgenerallyfindpositiveeffectsonstudentoutcomes.Butfunding
levelsweremuchhigherby1990thanearlier,andthemostsevereinequitiesin
schoolresourceshadbeenaddressed.Thus,theremayhavebeenlessscopefor
morerecent,adequacy-basedSFRstobenefitstudents.
Theliteratureregardingwhether“moneymatters”ineducation(Cardand
Krueger1992a;Hanushek1986,2003,2006;Burtless1996)iscontentiousanddoes
notofferclearguidance.Statefundingformulasarethemainpolicytoolavailableto
addressinequitiesinacademicoutcomes,sofundingshiftsderivingfromchangesin
theseformulasarethemostpolicy-relevantvariationinschoolresources.Thevery
limitedevidenceontheimpactsofearlySFRs,andthenear-totallackofevidence
regardingmorerecentreforms,representsamajorshortcomingintheliterature.
Weprovidethefirstevidencefromnationallyrepresentativedataregarding
theimpactofSFRsonstudentachievement.Weexploitlittle-useddatafromthe
NationalAssessmentofEducationalProgress(NAEP),alsoknownas“theNation’s
ReportCard.”NAEPhasadministeredtestsinmathandreadingtostate-
representativesamplesof100,000-200,000studentsinthefourthandeighthgrades
everytwotofouryearssince1990.Importantly,thetestshavebeenuniformacross
thecountryandovertime,facilitatingcomparisons.5
4CascioandReber(2013)andCascio,Gordon,andReber(2013)examinetheintroductionoffederalTitleIfundingtolow-incomeschoolsviathe1965ElementaryandSecondaryEducationAct.5Severalstudies(e.g.,DeeandJacob2011,LevineandSchanzenbach2009)exploitstatemeanscores.Microdataareavailableunderrestricted-usedatalicensesfromtheNationalCenterforEducationStatistics(NCES).WearegratefultoBruceKaplan,KatePashley,andFatihUnlufortheirassistanceinlocatingthecrosswalkfromtheolderNAEPdatatoschoolsanddistricts.
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WeusetheNAEPdatatoconstructastate-by-yearpanelofrelative
achievementinlow-incomeschooldistricts,coveringtheperiodfrom1990-2011.
Conveniently,thebeginningofourNAEPpanelcoincideswiththeonsetofthe
adequacyeraofschoolfinance,whichdatestothe1990KentuckyEducationReform
Act(KERA).Figure3showstheNAEPscoregap(instandarddeviationunits)
betweenlow-andhigh-incomedistrictsovertime,usingthesamedefinitionsasin
Figures1and2.Itshowsthatthetestscoregaphasbeenstableinstatesthatdidnot
implementreforms,buthasnarrowedinstatesthatimplementedreforms.
Figures2and3canbeseenaslong-differenceestimatesoftheeffectofSFRs,
andindicatethatSFRsledtoincreasesinfundingandtestscoresinlow-income
schooldistricts.Butthesepatternscouldbedrivenbyothertrendsthatdiffer
betweenstatesthatdidanddidnotimplementreforms.Totestthis,weuseanevent
studyframework,takingadvantageofplausiblyrandomvariationinthelocation
andtimingofpost-1990SFRs.Wefindnosignofsystematicchangesineither
fundingortestscoresintheperiodleadinguptoareform,supportingour
assumptionthatreformtimingisexogenous.Followingreforms,wedocumentsharp
increasesinstaterevenues,withlargerincreasesinlow-incomedistrictsand
smallerbutstillpositiveincreasesinhigh-incomedistricts.6Thesechangesoccur
quicklyafterreformevents,persistformanyyears,andarenotoffsetbyreductions
inlocalrevenues.Absoluteandrelativefundinginlow-incomedistrictsrisesby
approximately$1,200and$700perpupilperyear,respectively.
6Anecdotally,legislatorsfacingcourtorderstoincreasefundingtolow-incomedistrictsoftenrespondbyincreasingoverallfunding,asawayofdisguisingtheresultingredistribution.Reformsareassociatedwithsharpincreasesintotalstateeducationexpendituresandtaxcollections.
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Notsurprisingly,wefindnoimmediateeffectofreformsonachievement.But
wedofindclearchangesinachievementtrendsfollowingevents.Thesecumulate
overtime:Tenyearsafterareform,relativeachievementofstudentsinlow-income
districtshasrisenbyroughly0.1standarddeviation,approximatelyone-fifthofthe
baselinegapbetweenhigh-andlow-incomedistricts.Theimpliedimpactis0.12-
0.24standarddeviationsper$1,000perpupilinannualspending.Thisisatleast
twicetheimpactperdollarthatisimpliedbytheTennesseeProjectSTARclasssize
experiment.7Givenexistingestimatesoftherelationshipbetweentestscoresand
students’subsequentearnings,ourresultsimplythatthebenefitsofmarginal
increasesinschoolresourcesinlow-income,poorlyresourcedschooldistricts,in
termsofstudents’increasedeventualearnings,exceedthecosts.
Ourpapermakesthreeprimarycontributions.First,wepresentthefirst
comprehensiveevidenceregardingthefiscalimpactsofpost-1990,adequacySFRs.8
Weshowthatthesereformsleadtoincreasedprogressivityofstateaidandtotal
schoolfinance,withlittleifanyoftheadditionalstatefundingdissipatedthrough
reducedlocaleffortandwithnosignofreactionsthatreduceoverallfunding.
Second,wepresentthefirstnationalevidenceregardingtheeffectofany
financereformsontheachievementofarepresentativesampleofstudents.Our
estimatesimplythatadditionalfundingdistributedthroughcourt-mandated
changesinfinanceformulasishighlyproductiveinlow-incomeschooldistricts.7STARraisedcostsbyabout30%inK-3,andraisedtestscoresby0.17SDs(KruegerandWhitmore2001).CurrentspendingperpupilinTennesseeisaround$9,000,socomparableproportionalclasssizereductionswouldcostaround$2,700perpupilperyear.Theimpliedeffectisthusaround0.06SDsper$1,000perpupil.ThiscomparisonimplicitlyassumesthatmaintainingthesmallerSTARclasssizesbeyond3rdgradewouldyieldnoadditionalgrowthintestscores.8Sims(2011a)andCorcoranandEvans(2015)contrastfiscalimpactsofequityandadequacyreforms.Buttheirsamplesendin2002,andthusreflectonlythebeginningoftheadequacyera.
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Finally,wepresentthefirstanalysisoftheimpactoffinancereformson
overalleducationalequity.Wefindnodiscernableeffectofreformsoneitherthe
gapinachievementbetweenhigh-andlow-incomestudentsortheminority-white
gap.Thisisnotbecausefundingisunproductive.Rather,low-incomeandminority
studentsarenotveryhighlyconcentratedinschooldistrictswithlowmean
incomes,soarenotcloselytargetedbydistrict-basedfinancereforms.Thus,while
ouranalysissuggeststhatfinancereformscanbequiteeffectiveatreducing
between-districtinequities,otherpolicytoolsaimedatwithin-districtresourceand
achievementgapswillbeneededtoaddressoverallequityconcerns.
I. Schoolfinancereforms9
Historically,Americanpublicschoolswerelocallymanagedandfinanced
primarilyvialocalpropertytaxes.Asschooldistrictsvarywidelyinboththeirtax
basesandtheirvoters’willingnesstotaxthemselvestofundschools,thismeantthat
schoolresourcesvariedsubstantiallyacrossdistricts.
Inthe1960s,agroupoflegalscholarsarguedthatlocalschoolfinance
violatesfederalandstateconstitutionalprovisionsthatguaranteeequalaccessto
publicservices(see,e.g.,Wise1967;Horowitz1966;Kirp1968;andCoons,Clune,
andSugarman1970).Advocatesbroughtandwonsuitsinmanystatesdemanding
moreequitableschoolfinancesystems;inotherstates,legislaturesactedwithout
courtdecisions(oftentostaveoffpotentialrulings).10
9OurdiscussionheredrawsheavilyonKoskiandHahnel(2015).10AnearlyU.S.SupremeCourtdecision,SanAntonioIndependentSchoolDistrictv.Rodriguez(411US1,1973)heldthateducationisnotafundamentalrightundertheU.S.Constitution.Subsequentsuitsfocusedonstateconstitutions,whichoftenarticulateresponsibilityforasystemofpubliceducation.
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Theresultingfinanceregimesofteninvolvedsubstantialincreasesinstate
transferstodistrictsthatdependedeitheronlocalfiscalcapacity(“power
equalization”)orrealizedlocalrevenues(“matching”or“variable”grants).An
extensive“fiscalfederalism”literatureexaminestheeffectsofthesereformsonthe
distributionofschoolfunding(see,e.g.,HanushekandLindseth,2009;Corcoranand
Evans,2015;CardandPayne,2002;Murray,Evans,andSchwab,1998).Aparticular
focusiswhetherformulasthatraisethemarginallocalcostofadditionalschool
spendingaffectvoters’choicesaboutthelocalspendinglevel(e.g.,Hoxby2001).
Asecondwaveoffinancereforms—thefocusofthispaper—iscommonly
datedtoa1989KentuckySupremeCourtruling.Here,theCourtfoundthatthestate
constitution,whichasinmanyotherstatesdictatesan“efficientsystem”ofpublic
schools,requiresthat“[e]achchild,everychild,…mustbeprovidedwithanequal
opportunitytohaveanadequateeducation”(Rosev.CouncilforBetterEducation11;
emphasisinoriginal).Therulingemphasizedthatequalfundingwasnotsufficient,
andarticulatedastandardclosertoequalityofoutcomesforstudentsinlow-income
districts(e.g.,“sufficientlevelsofacademicorvocationalskillstoenablepublic
schoolstudentstocompetefavorablywiththeircounterpartsinsurroundingstates,
inacademicsorinthejobmarket”).TheKentuckylegislaturerespondedwiththe
KentuckyEducationReformActof1990(KERA),whichrevampedthestate’s
educationalfinance,governance,andcurriculum.Clark(2003)andFlanaganand
Murray(2004)findKERAsubstantiallyincreasedspendinginlow-incomedistricts.
11790SW2d186.Rosewasnotthefirstadequacyruling,butearlierrulingsattractedlessattention.
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Since1990,courtsinmanyotherstateshavefoundadequacyrequirements
intheirownconstitutions.Inmanycasesreformshaveaimedathigherspendingin
low-incomethaninhigh-incomedistricts,tocompensatefortheout-of-school
disadvantagesthatlow-incomestudentsface.12
Reformadvocateshaveconsciouslyimitatedthepushforschool
desegregationeffortinthe1950s-1980s,andlikethatmovementhaveoperated
opportunistically,takingadvantageofvariationinlegalprecedentandthe
availabilityofsympatheticjudgestoadvanceanationaleffort.Courtsindifferent
stateshaveinterpretedseeminglysimilarstateconstitutionallanguagequite
differently,eitherimposingorrulingoutadequacyrequirements.13Thereislittle
reasontothinkthatthecasesarebroughtinresponsetopoliticalorother
developmentsthatwouldhaveindependentlyaffectedachievementgapsinastate.
Moreover,thevagariesofthejudicialprocess—casesaretypicallyappealedupward
throughseverallevelsofreview—anddecisionsinsomestatestoimplement
legislativereformstosettleongoingcasesorforestallfearedcourtrulingsgenerate
additionalquasi-randomvariationintiming.Ouranalyticstrategy,developedbelow,
ispremisedontheassumptionthatreformtimingisuncorrelatedwithother
determinantsoftrendsin(relative)spendingandachievementinlow-income
districts.WepresentevidenceinsupportofthisassumptioninSectionsIVandV.
12Asmallindustryhasdevelopedtocalculatethespendinglevelneededtosatisfyanadequacystandard.See,e.g.,DownesandSteifel(2015)andDuncombe,Nguyen-Hoang,andYinger(2015).13Forexample,theIllinoisSupremeCourthasfoundthatschoolfinancereformcasesarenotjusticiablebythecourtsandmustbeaddressedinsteadbythelegislature(672N.E.2d1178).Therelevantclauseinthestate’sconstitution(“anefficientsystemofhigh-qualitypubliceducationalinstitutionsandservices”)issimilartothatinOhio(“athoroughandefficientsystemofcommonschoolsthroughouttheState”),wherethecourtshaveintervened.
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WehaveattemptedtoidentifyallmajorSFRsbetween1990and2011.We
beganwithlistsofcourt-orderedreformscompiledbyJacksonetal.(2016)and
CorcoranandEvans(2015).Wesupplementedthesewithourownresearchinto
casehistories,andupdatedthemthrough2011.Wealsotabulatedmajorlegislative
SFRs.Insomeimportantcases(e.g.,Colorado,California),legislaturesreformed
financesystemswithoutpriorcourtdecisions,oftentoforestalladversejudgments
inthreatenedorongoinglawsuits.Ourprimaryanalysesincludethese,thoughwe
alsopresentresultsthatfocusexclusivelyoncourtorders.
AppendixTableA1presentsacompletelistofoureventsandcomparesitto
thoseusedinotherstudies.Weidentifyatotalof64schoolfinancereformeventsin
21statesbetween1990and2011.1439(61%)involvecourtorders;theremainder
arelegislativeactionswithoutamajorcourtorderinthesameyear.
Figure4showsthedistributionofeventsovertime,withlegislativeSFRs
indicatedbydarkerbars.Therehavebeensubstantiallymorecourt-orderedSFRs
duringtheadequacyerathanintheprior,morestudiedequityera.15Figure5shows
thegeographicdistribution.Stateswitheventsarequitegeographicallydiverse,
thoughreformsarerareinthedeepSouthandupperMidwest.
18stateshadmultipleeventsinourperiod.Theseweregenerallyclosely
spaced:60%werethreeorfeweryearsapart.Inthesecases,wesuspectthatonly
onegeneratedamajorchangeinthestate’sfinancerulesandthatothersare
proceduralsteps(e.g.,courtordersthatweredisregardedorlegislationchanges
14Ourpanelexcludesthe1989RosedecisionbutincludesKERA,thelegislature’sresponsein1990.15Jacksonetal.(2016)code15court-orderedSFRsfrom1971through1989,and48sincethen.Wecodeafewcasesdifferentlythanhaveearlierauthors.ThesearediscussedintheAppendix.
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thatwerelaterfoundinadequate).Ouranalyticalstrategyisbuiltwiththisideain
mind,thoughourresultsarenotsensitivetohowmultipleeventsaretreated.
Aswithearlierequityreforms,statesunderadequacyordershavevariedin
thefinancesystemsthattheyhaveadopted.Despitethisheterogeneity,thereare
twoimportantreasonstoexpectthatadequacyreformshaddifferentimpactsonthe
levelanddistributionofschoolfundingthandidearlierequityreforms.First,equity
reformsoftenfocusedondistricts’propertytaxbases,whereadequacyreforms
focusedonstudentdisadvantage;thetwomaynotbestronglycorrelated(Fischel
1989).Second,whereastatemightrespondtoanequityorderby“levelingdown”to
stingybutequalfunding,thiswouldnotsatisfyanadequacymandate.Statesseem
insteadtohaveincreasedfundingtoalldistrictstomeetadequacyrequirements
whilestillallowinghigher-incomedistrictstodifferentiatethemselves.
Overall,then,weexpectthatadequacyreformscausedhigherspending,in
generalandparticularlyinlow-incomedistricts,thandidequityreforms,but
perhapsalsoyieldedsmallerreductionsinthebetween-districtdispersion(Baker
andGreen,2015;DownesandStiefel,2015).Weconfirmthesepredictionsbelow.
II. Analyticapproach
Theprimarychallengeinestimatingthecausaleffectofadequacyreformsis
thatthesereformsmaybecorrelatedwithotherfactorsthataffectrealizedschool
financeorstudentoutcomes.Animportantconcernisthatstatesthataremore
aggressiveintargetingfundingtolow-incomeschooldistrictsmayalsodifferin
otherways—theymayhavebetterdevelopedsocialwelfaresystems,more
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equitablehousingpricedistributions,ordifferentapproachestoregulatingschool
quality(Hanushek,Rivkin,andTaylor1996a,b).
Toaddressthis,weleveragevariationinthetimingofreformeventsinan
event-studyframework.Ourstrategyisbasedontheideathatstateswithoutevents
inaparticularyearformausefulcounterfactualforstatesthatdohaveeventsin
thatyear,afteraccountingforfixeddifferencesbetweenthestatesandforcommon
timeeffects.Thekeyassumptionisthattheexacttimingofeventsisasgoodas
random.Wethinkthisisplausible,giventheidiosyncrasiesofjudicialprocesses
discussedabove.Anattractivefeatureofourapproachisthatitbuildsinteststhat
shouldidentifylikelyviolationsofthisassumption.
Oursimplesteventstudyspecificationmodelseventsaspermanent,
immediateshiftsinoutcomesrelativetootherstates:
(1) !!" = !! + !! + 1 ! > !!∗ !!"#$ + !!" .
Here,!!"representssomesummaryofthedistributionoffundingorachievementin
statesinyeart.Wediscussourparticularmeasuresbelow.!!and!!represent
stateandyeareffects,respectively.!!∗isthedateonwhichstates’seventoccurred.
(Fornow,weassumethateachstatejustoneevent;thistermissettozeroforstates
thatdonothaveevents.)Thecoefficientestimate!!"#$representsthechangein
theoutcomefollowingtheevent.
SFRsmaynotaffect!!"immediately,butmaydevelopmoregradually.Thisis
particularlytrueforstudentachievementoutcomes,astheachievementofastudent
inyeartlikelydependsinpartonthequalityoftheschoolingshereceivedinprior
years.Inaddition,ifeventtimingisnon-random,stateswitheventsmaydiverge
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fromstateswithouteventsevenbeforethedateoftheevent.Toaccommodatethese
ideas,weaddtwotrendtermsto(1):
(2) !!" = !! + !! + 1 ! > !!∗ !!"#$ + 1 ! > !!∗ ! − !!∗ !!!!"#$% + ! −
!!∗ !!"#$% + !!" .
!!!!"#$%capturesdelayedeventeffectsandrepresentstheannualchangein
outcomesinstatesafter!!∗,relativetothesamestatepriortotheevent.!!"#$% ,
whichisidentifiedfromchangesinsrelativetootherstatesinyearspriorto!!∗,
representsafalsificationtest:!!"#$% ≠ 0wouldindicatethateventtimingis
meaningfullynon-random.
Wealsoestimatenon-parametricmodelsthatdonotconstrainthephase-in
andpriortrendeffectstobelinear:
(3) !!" = !! + !! + 1 ! = !!∗ + !!!"#!!!!"# !! + !!" .
Here, rrepresentstheeffectofaneventinyear!!∗onoutcomesryearslater(or
previously,forr
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differentfromzero,andinthiscaseitappearstobeanidiosyncraticblipinasingle
β-rcoefficient(seeFigure12).Thissupportsouridentifyingassumption.
Whenweexaminefinanceoutcomes,allofthepost-eventeffectappearstobe
nearlyimmediate,sowefocusonthesimplerspecification(1).Bycontrast,inour
studentachievementanalysis,the“jump”isneverdistinguishablefromzero,andall
oftheeffectthatweestimateoperatesthroughthe!!!!"#$%coefficient.Wethus
emphasizespecificationsthatallowforaphase-ineffectbutnopost-eventjump.In
eachcase,thesesimplespecificationsfitthenon-parametricresultsquitewell.
Difference-in-differencesandtriple-differences
Theeventstudymethodologyoutlinedaboveisaformofdifference-in-
differences,identifyingtheeffectofeventsfromdeviationsinthetrendin“treated”
statesrelativetostatesthathavenotyethadevents.Theidentifyingassumptionis
thatwithoutfinancereforms,outcomeswouldhaveevolvedinparallelintreated
anduntreatedstates.Hanusheketal.(1996a,b)arecriticalofthisassumptionwith
regardstotheimpactsofschoolspendinginstate-by-yearpanels,arguingthatthe
paralleltrendassumptionisunlikelytohold,biasingtheDDestimates.
Accordingly,whilewepresentbelowDDestimateswithmeanspendingor
meantestscoresinastateastheoutcome,webelievethatmorecredibleestimates
oftheeffectoffundingreformscanbeobtainedfromtriple-differencemodelsthat
comparetheimpactsofSFReventsonhigh-andlow-incomedistrictsinastate.We
implementtheseusingtheDDmethodologyabovebyusingasthedependent
variable!!"ameasureoftheachievementoflow-incomedistrictsinastaterelative
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tothatinhigher-incomedistricts.Withthistypeofdependentvariable,theevent
studystrategyisrobusttoarbitrarystate-by-yearshockstospendingor
achievement,solongastheyhavesimilareffectsondistrictsatdifferentincome
levels.Theidentifyingassumptionisthattherelativeoutcomesoflow-income
districtswouldhavefollowedparalleltrendsacrossstatesintheabsenceofSFRs.
Weconsidertwomeasuresofrelativespendingorachievementinlow-
incomedistricts.First,weusethegapbetweendistrictsinthetopandbottom
quintilesofthestateincomedistribution,asinFigures2and3.Thesequintilegaps
arequitenoisy,inpartbecausetheydiscardinformationonthemiddle60%of
districts.Wethusemphasizeasecondmeasure,theslopeofdistrict-leveloutcomes
withrespecttologaverageincomeacrossalldistrictsinthestate.16Amorenegative
slopecorrespondstohigherrelativeoutcomesinlow-incomedistricts.Appendix
FigureA2repeatsthelong-differenceanalysisfromFigures2and3,thistimeusing
ourslopemeasureinplaceofthequintilegaps.Resultsareevenstronger.
Toillustrate,Figure6showsthescatterplotofperpupilstatetransfersto
districtsagainstlogmeandistrictincome(measuredin1990)foreachdistrictin
Ohio,firstin1990andthenin2011.Asthefigureshows,statetransfersrose
dramaticallyoverthisperiod,particularlyinthelower-incomedistricts.Weoverlay
twofittedseriesontopofthis:Oneshowsmeantransfersacrossalldistrictsineach
incomequintile,andtheothershowstheslopeasdescribedabove.Inthiscase,the
16Specifically,weregressdistrict-levelspendingperpupilormeanachievementonlogmeanincome,controllingforlogenrollment.Theregressionisestimatedseparatelyforeachstateandyear,andinachievementmodelsforeachsubjectandgrade.Thedistrictlogincomecoefficientsareusedas!!"forsubsequentanalysesatthestate-year-(subject-grade)level.SeetheAppendixforfurtherdetail.
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log-linearspecificationfitsthequintilemeansfairlywell.Acrossstates,theslopeis
correlated-0.78withthefirst-quintile/fifth-quintilegap.
WeshowbelowthatSFRsleadtohigherabsoluterevenuesinalldistrictsina
stateandtohigherrelativerevenuesinlow-incomedistricts,asseenforOhioin
Figure6.Eachofthesecouldaffecttherelativeachievementofstudentsinlow-
incomedistricts.First,ifmoneymatters,thentheincreaseinrelativespending
shouldraiselow-incomedistricts’achievement.Second,themarginaleffectofextra
fundsmaybehigherinlow-incomedistricts,perhapsduetodecliningmarginal
productivityofadditionalresources.Ifso,evenanacross-the-boardspending
increasewouldraiserelativetheirrelativeachievement.Giventhesetwochannels,
andtimingissuesthatwillbecomeclearbelow,wearecautiousinconvertingour
estimatedeffectsonachievementintoestimatesofoutputperdollar,asitisnot
clearwhatistheappropriatedenominatorforourDDDtreatmenteffects.
Eventstudieswithmultipleevents
Asnotedabove,manystateshadmultipleevents(courtordersorlegislation)
overourperiod.Unfortunately,thereisnoacceptedstrategyforconductingevent
studieswithmultipleeventsperunit.
Ohioillustratesboththechallengeandourproposedsolution.Thestate
SupremeCourtruledfourtimesontheDeRolphv.Statecase,in1997,2000,2001,
and2002.The1997rulingdeclaredthestate’sfinancesystemunconstitutionalon
adequacygrounds,andspecificallyrejectedthestate’srelianceonlocalproperty
taxes.TheCourtordereda“completesystematicoverhaul”oftheschoolfunding
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17
system.In2000,theCourtdeterminedthatthelegislaturehadfailedtoactandthat
fundinglevelsremainedinadequate.Thesameyear,thelegislaturerevisedthe
system,andasubsequentrulingin2001determinedthatthenewsystem,witha
fewminorchanges,satisfiedconstitutionalrequirements.Thisdecisionwas
reversedin2002,bythesameCourt(albeitwithadifferentmakeupofjudges),and
thelegislatureorderedtomakefurtherchanges.Toourknowledge,thelegislature
didnothingtocomplywiththis.
OurreformdatabaseincludesOhioeventsin1997,2000,and2002.Basedon
theabovecasehistory,wemightexpectonlythe2000eventtobeassociatedwith
majorchangesinschoolfinanceinOhio.Butthedatatelladifferentstory.Figure7
showsthetimeseriesofourtwomeasuresoftheprogressivityofstateaidinOhio
(withtheslopemeasureinvertedforcomparability):Thedifferenceinaveragestate
transfersperpupilbetweenthelowest-incomeandhighest-incomefifthsofOhio
schooldistricts(solid)andtheslopeofstatetransferswithrespecttologincome,
multipliedby-1(dashed).Verticallinesindicatethereformevents.Thefigure
showsthatstatetransferswereprogressivein1990andslowlybecamemoresoin
thefirstfewyearsofourdata.Around1998,thetrendbecamenotablysteeper,and
by2002averagestateaidperpupilwas$4,851higherinlow-incomethaninhigh-
incomedistricts.Ifanything,relativefundinghasdeclinedsince2002.Thispattern
appearsconsistentwithagradualreactiontotheinitial1997ruling.Thereisless
visualevidenceofthe2000event,whichdidnotinterrupttheprevioustrend,while
the2002rulingseemstocoincidewithanendtotheincreasesinprogressivity.
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18
BasedonthepatternsinOhioandelsewhere,weadoptedtwoanalytical
decisionsforourprimaryestimates.First,wechooseasingleeventineachstate.
Ourideahereisthatwhenstateshavemultipleevents,theyoftenrepresent
jockeyingbetweenthelegislatureandthecourtswithonlyminorchangesinschool
financeuntilthelegislaturefinallyenactsamajorreform,andthencontinued
jockeyingafterwardasadvocatescontinuetopushforsmalleradditionalchanges.
Second,wedonotrelyonreviewsofcasehistoriestoidentifythe
consequentialevents,astherhetoricincourtordersandpreamblestobillsisoften
(asinOhio)misleadingaboutthemagnitudeofthechangebeingmade.Rather,we
usethestateaiddatatoidentifyaregimechangeintheprogressivityofastate’s
financesystem,relyingonmethodsfortheidentificationofchangepointsintime
seriesdata(e.g.,Bai1997;seealsoCard,Mas,andRothstein2008).
Specifically,let!!"beourslopemeasureoftheprogressivityofstateaid.For
eachstateandeachpotentialeventdate!!∗,weestimateatimeseriesregression
usingastheonlyexplanatoryvariableanindicatorforobservationsafterthatdate:
(4) !!" = ! + 1 ! > !!∗ ! + !!" .
Weselectthedatethatyieldsthelargesttstatisticfor!–orequivalentlythe
smallestmeansquarederror–forthistimeseriesregression.17Wetreatthe
selecteddateasthesingleeventinstates.Bai(1997)showsthatthismethodis
super-consistent(withfasterthan !convergence)forthelocationofastructural
breakinatimeseries,permittinginferenceregardingthemagnitudeofthebreakto
treatitslocationasknown.
17Werestrictattentiontot*forwhichtheestimated!hastheexpectedsign.
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19
Wepresentestimatesfromtwoadditionalapproachestomultipleevents.
Oneincludesallevents,withoutjudgmentabouttheirrelativeimportance.We
createaseparatecopyofthetimeseriesforthestateforeachevent,foreachcopy
usingadifferentvalueof!!∗.Wethenstackthesecopies,replacingthestateeffectsin
equations(1)-(3)withstate-by-event-copyeffects.18InMonteCarlosimulations,
thismethodworkswelltoidentifytheaverageeffectofeventsbothwheneach
eventhasthesameeffectandwhenonlyoneeventinastatehasanon-zeroeffect.
Ourfinalapproachfollowsthepriorliteraturebyfocusingontheinitialcourt
orderineachstate.Pastauthorshavearguedthatthetimingofinitialcourtordersis
effectivelyrandombutthatlegislativeeventsandsubsequentcourtordersmaynot
be.Thedrawbacktothisapproachisthattherecanbelonglagsbetweentheinitial
courtorderandtheimplementationofareform.Itisthusbettersuitedtosimple
modelslike(1)thatarenothighlysensitivetomis-timingthestructuralbreak—
mostpastworkusingthisapproachhasfocusedonsuchmodels—thantomore
flexiblemodelslikeournon-parametricspecification(3).
Inappropriatespecifications,resultsarequiterobustacrossallthree
methods.Accordingly,wedonotviewmultipleeventsasamajorissueinpractice.
III. Data
Ouranalysisdrawsondatafromseveralsources.Webeginwithour
databaseofstateSFRevents,discussedabove.Wemergethistodistrict-levelschool
financedata,fromtheNationalCenterforEducationStatistics’(NCES)annual
18Resultsareunchangedwhendataarereweightedtooffsettheoverrepresentationofstateswithmultipleevents.
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20
censusofschooldistricts(theCommonCoreofData,orCCD,districtfinancefiles,
alsoknownasthe“F-33”survey)andtheCensusofGovernments;meanhousehold
incomebydistrictfromthe1990Census;andNAEPachievement.
TheCCDdistrictfinancedatareportenrollment,revenuesandexpenditures
annuallyforeachlocaleducationagency(LEA).19Weconvertalldollarfiguresto
2013dollarsperpupil,andexcludedistrictswithhighlyvolatileenrollmentor
implausibleper-pupil-funding.Detailsareintheappendix.
OurstudentoutcomemeasurescomefromtheNationalAssessmentof
EducationalProgress(NAEP).Weuserestricted-usemicrodatafromthe“State
NAEP,”designedtoproducestate-representativesamples.StateNAEPbeganin
1990,with42statesparticipating.Ithasbeenadministeredroughlyeverytwoyears
since.Since2003,allstateshaveparticipatedin4thand8thgradeassessmentsin
mathandreadingineveryodd-numberedyear.20Table1showstheschedule.Tests
areadministeredtoaround100,000students(moreinlateryears)ineachsubject-
grade-year.Theseconsistofrepresentativesamplesofabout2,500studentsper
state,spreadacrossabout100schools.
TheNAEPusesaconsistentscoringscaleacrossyearsforeachsubjectand
grade.Westandardizescorestohavemeanzeroandstandarddeviationoneinthe
firstyearthatthetestwasgivenforthegradeandsubject,butallowboththemean
19Censusdataareavailablein1989-90and1991-92,andannuallysince1994-95.WeusesamplesfromtheCensusBureau’sAnnualSurveyofGovernmentFinancesfor1992-93and1993-94.20TheNAEPalsotests12thgraders,butsamplesaresmaller,andothersubjects.
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21
andvariancetoevolveafterward.Wethenaggregatetothedistrict-year-grade-
subjectlevelandmergetotheCCDandSDDB.21
Table2apresentsdistrict-levelsummarystatistics,poolingdatafrom1990-
2011.Table2bpresentssummarystatisticsforthestate-yearpanel.
IV. Financereformsandschoolfinance
WebeginourempiricalanalysisbydocumentingtheimplicationsofSFR
eventsforschoolfinance.WeusetheapproachdiscussedinSectionIItoidentifya
singleSFReventineachstate,selectingamongcandidateeventstheonethatbest
explainsthetimeseriesofthestateaid–logdistrictincomeslopeinthestate.
Figure8,panelAgraphseventstudyresultsforaveragestatetransfersper
pupilinthestate,poolingalldistricts.Wepresentanumberofplotsofthisbasic
form.Thesolidlinepresentsestimatesofthenon-parametriceventstudy
specification(3),whiledottedlinesshowpointwise95%confidenceintervals.The
dashedlineshowstheparametricspecification(2).
Pointestimatesindicatethataveragestatetransferstodistrictsriseinthe
yearsleadinguptoanevent,thoughthiscouldbejustsamplingerror–thep-value
forequalityacrossallyearspriortotheeventsis0.31.Bycontrast,inthefouryears
followingtheeventaveragestatetransfersrisebyroughly$1,000.Theydecline
somewhatinsubsequentyears,buteven15yearsafterthefocaleventremain
approximately$500abovewhatwouldhavebeenexpectedwithouttheevent.The
differencesfromtheeventyeararesignificantbothcollectively(p
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22
individuallyforrelativeyears1-10.Theparametricspecificationfitsthe
nonparametricresultswell.PanelBofFigure8repeatstheexercise,thistimeusing
totalper-pupilrevenues(inclusiveoflocalrevenuesandfederaltransfers)asthe
dependentvariable.Thepatternisquitesimilarhere,withlittleindicationthat
increasesinstaterevenuesareoffsetbyreductionsinlocaleffortonaverage.
Columns1and3ofTable3presentcoefficientsfromoursimplestone-
parametereventstudyspecification(1),firstforstaterevenuesandthenfortotal
revenues.Eventsareassociatedwithincreasesinstateaidof$912perpupil,and
withslightlysmallerincreases($829perpupil)intotalrevenues.Columns2and4
presentthethree-parameterspecification(2).Post-eventeffectsarequitesimilarto
thoseseenintheone-parametermodels;whilepointestimatesindicatethatthey
trenddownoversubsequentyears,thesearenotdistinguishablefromzero.In
column2,theupwardtrendprecedingeventsthatwasvisibleinFigure8aissmall
andinsignificant,supportingourassumptionthateventtimingisrandom.
Theseresultspreviewageneralpatternweseethroughoutourfinance
analyses.Nonparametricmodelsshowalargejumpoverthefirstthreetofouryears
followingtheevent,withrelativelysmalltrendsbeforeandafter.Pre-eventtrends
areneverstatisticallysignificant,andwhilewecangenerallyrejectzeroeffectof
eventsonallpost-eventoutcomes,wecannever(inthethree-parametermodel)
rejectasinglejumpfollowingtheeventthatpersistsunchangedthereafter.
Accordingly,wefocusontheone-parametermodelforsubsequentfinanceanalyses.
Inadditionalanalysesofstatebudgets,(AppendixTableA2)wehavefound
noindicationthatgrowthineducationalspendingfollowingeventscrowdsoutstate
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23
spendingonotherprograms;rather,SFRsareassociatedwithincreasesinstatetax
collectionslargeenoughtofullyfundtheincreaseinstatetransferstodistricts.
WeturnnexttoexaminingtheimpactofSFRsonthedistributionoffunding
acrossschooldistricts.Figure9presentseventstudyanalyses,similartothosein
Figure8,foraveragestateaidandtotalrevenuesperpupilindistrictsinthetopand
bottomquintilesofthestateincomedistribution.Thereisagainsomeindicationof
pre-eventupwardtrendsinstaterevenues,butagainwecannotrejectthenull
hypothesisofzeropre-eventdifferences.Bothlow-andhigh-incomedistrictssee
increasesinstateandtotalrevenuesfollowingtheevent,buttheincreasesare
largerinlow-incomedistricts:Roughly$1,300bythe4thpost-eventyear,vs.less
thanhalfthat(andnotrobustlysignificant)inhigh-incomedistricts.Thoughout-
yearestimatesarenoisy,impactsappeartopersistthroughtheendofoursample.
Patternsfortotalrevenuesareverysimilartothoseforstaterevenues,andshow
littlesignthatstaterevenueincreasesareoffsetbyreductionsinlocalrevenues.
PanelsBandCofTable3presenttheparametricestimatesforthelowest-
andhighest-incomedistricts.Averagestatefundingis$1,225higheraftereventsin
firstquintiledistrictsand$527(notsignificant)higherinfifthquintiledistricts;in
eachcase,totalrevenuechangesareofsimilarmagnitude,andthemoreflexible
specificationyieldssimilarresults.
Figure10showsestimatesofimpactsontheprogressivityoftotalrevenues,
usinginthetoppanelthedifferenceinfundingbetweenbottom-andtop-quintile
districtsandinthelowerpaneltheslopeoffundingwithrespecttologdistrict
income.ParametricmodelsfortheseoutcomesareshowninColumn4ofTable4.
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24
Usingeachmeasure,weseesharpincreasesinrelativestatefundingforlow-income
districtsfollowingeventsthataresustained(thoughnotalwaysprecisely
estimated)formanyyears.Innocaseisthereanysignofapre-eventtrendthat
wouldsuggestaviolationofourrandomtimingassumption.Noristhereanysignin
Table4thatincreasedprogressivityofstateaidisoffsetbylocalrevenues.22
Anaturalquestionishowtheadditionalfundsarespent.Table5presents
event-studycoefficientsfromourone-parametermodelforper-pupilrevenuesand
spendinginvariouscategories.ThereisnoapparentimpactofSFRsonlocalor
federalrevenues.WeseesubstantialimpactsofSFRsonaverageinstructional
spending,bothoverallandinQ1districts(columns2and3).Wealsoseeeffectson
teachersperpupil,suggestingthatdistrictsuseadditionalfundstoreduceclasssize,
thoughwefindnosignofimpactsonteacherpay.23Wealsoseelargeincreasesin
non-instructionalexpenditures,particularlycapitaloutlays.
Columns4and5showresultsforrelativespendinginlow-incomedistricts.
Littleoftheincreaseinrelativefundinggoestoinstructionalexpenditures,while
roughlyhalfgoestocapitalspending.Thecapitalspendingeffectisnotsurprising;
manylawsuitsspecificallyconcerndreadfulconditionsinlow-incomeschools,and
SFRremediesoftencreatedfundstosupportrenovationofschoolsinpoorshape.24
22WhenweestimatespecificationssimilartoCardandPayne’s(2002)closelyrelatedanalysisofearlierSFRs(AppendixTableA3),estimatedSFReffectsareslightlylargerbutimprecise,andwellwithintheearlierconfidenceintervals.WhereCardandPaynefindthattotalrevenuesrisebyabout$0.50perextra$1instateaid,ourestimatesindicatemuchmorestickinessfortherecentreforms.23Usingadifferentresearchdesign,Sims(2011b)findseffectsofSFRsonteacherpay.24NeilsonandZimmerman(2014)findthatschoolreconstructioncausesincreasesinstudentachievement.Cellinietal.(2010)andMartorell,Stange,andMcFarlin(2015)failtofindsignificanteffects,buteachstudyisunder-poweredtodetecteffectsofplausiblemagnitude.
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25
V. Financereformsanddistrict-levelstudentachievement
Wecannowturntoourmainanalysis,examiningtheeffectofSFRson
studentachievement.Theaboveresultsestablishthatreformeventsareassociated
withsharp,immediateincreasesintheprogressivityofschoolfinance,withabsolute
andrelativeincreasesinrevenuesinlow-incomeschooldistricts.Ifadditional
fundingisproductive,wemightexpecttoseeimpactsonstudentoutcomes.
Wherethe!!"schoolfinancemeasuresformedastate-by-yearpanel,fortest
scoreswehavetwoadditionaldimensions:Gradeandsubject.Wereplacetheyear
fixedeffects(!!)in(1)-(3)withsubject-grade-yeareffects.Thesecaptureany
differencesintestsbetweenadministrations,aswellaschangesinstudent
performancebygradeand/orsubjectthatarecommonacrossstates.Toavoid
confoundingfromstate-levelshocks,wefocusonDDDspecificationsthatusethe
achievementgapbetweenlow-andhigh-incomedistrictsasthedependentvariable.
Sharp,permanentchangesinfunding,ifusedproductively,shouldincrease
theflowofeducationalservices.Achievementiscumulative,sotheseservicesare
unlikelytohaveimmediateimpactsontestscores,butshouldraisescoresgradually
asstudentsareexposedforlonger.Effectsshouldgrowatleastuntilstudentshave
beenexposedtothenewfundinglevelsfortheirentirecareers.Theymayeven
continuetogrowbeyondthispoint.Forexample,considerastatethatrespondstoa
courtorderbycreatinganewpermanentfacilitytofundseveralschoolrenovation
andconstructionprojectseachyear.Initially,onlyafewstudentsbenefit,butover
timegrowingsharesofstudentsareexposedtofundedprojects.Insofarasbetter
facilitiespromotestudentlearning,achievementeffectswouldcontinuetogrow
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26
untilseveralyearsafterthelastprojectiscomplete,potentiallydecadesafterthe
initialpolicychange.Wethusemphasizethephase-incoefficientfromequation(2)
astheprimarymeasureofSFReffectsontestscores.
Figure11presentsourevent-studyanalysisoftheslopeofachievementwith
respecttodistrictincome.Asbefore,wepresentnon-parametricresults(equation
3)asasolidlineandestimatesofourthree-parametermodel(equation2)asa
dashedline.Thereisnoindicationofadifferentialtrendinreformstatespriorto
events.Followingevents,thenon-parametricseriesdoesnotreactimmediately,but
beginstrendingnoticeablydownwardstartinginaboutthefifthpost-eventyear.
Thedownwardtrendcontinuesthroughtheendofoursample.25
Table6presentsparametricestimates.WebegininColumn1withourthree-
parametermodel,asshowninFigure11.Again,theestimatedpre-eventtrendis
essentiallyzero,andthepost-eventjumpisalsosmall,butthepost-eventchangein
trendislargeandstatisticallysignificant.Column2presentsaspecificationthat
discardstheothertwocoefficients.Resultsarequitesimilar.Theestimatedchange
intheslopeis-0.010peryear.Thisimpliesthateachyearafteranevent,adistrict
withlogmeanincomeoneunit(abouttwothirds)belowthestateaverageseesits
scoresriserelativetothestateaverageby0.010standarddeviations,accumulating
to0.10SDsovertenyears.Thisisquantitativelymeaningful–onaverageinour
sampletheslopeoftestscoreswithrespecttologincomeis0.96soSFRsreducethis
gradientbyapproximatelyone-tenthwithintenyears.
25ThesawtoothpatternattheendofthesamplelikelyreflectsthebiannualNAEPtestingschedule.
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27
Asdiscussedabove,thepatternofgraduallygrowingeffectsinFigure11is
consistentwithaviewofachievementasastockreflectingaccumulatedpastinput
flows.Thepatterndeviatesfromexpectationsinonerespect,however:Thereisno
indicationthatthephase-inoftheeffectslowsfiveornineyearsaftertheevent,
whenthe4thand8thgraders,respectively,willhaveattendedschoolsolelyinthe
post-eventperiod.26Thismayreflecttheuseofsomeadditionalfundsfordurable
investments,asdiscussedabove.Wedonothaveenoughprecision,however,torule
outaflatteningoftheeffectattheexpectedtime.
Figure12presentsestimatedtestscoreimpactsforthelowest-andhighest-
incomedistricts.Theeffectsontheincomegradientaredrivenbydramatic
increasesintestscoresinthelowest-incomedistricts.27Inhigher-incomedistricts,
thereislittlesignofasystematicpost-eventchange.Parametricestimatesare
showninColumns3and4ofTable6;Column5showsthattheimpactofeventson
thetestscoregapbetweenbottom-andtop-quintiledistrictsis0.008SDsperyear.
Thisgrowswhentrendtermsareincluded(column6).Thegapinmeanlogincomes
betweenthetopandbottomquintilesaverages0.65,sothequintilepointestimateis
largerthanwhatweobtainforourincomeslopemeasureincolumns1-2.Our
earlierfinanceanalysesalsoindicatedlargereffectsforquintilegapsthanforslopes.
AppendixFigureA3presentsestimatesofthephase-incoefficientforallfive
quintiles.Onlythefirstquintileeffectislargeordistinguishablefromzero.Theratio
26Wehaveestimatedseparatenon-parametricmodelsfor4thand8thgradescores.Bothsetsofeffectsgrowroughlylinearlythroughtheendofourpanels.SeeAppendixFigureA4.27Forthelowest-incomedistricts(Figure12A),wecanrejectthenullhypothesisofzeropre-eventeffects.Thisisdrivenbywhatappeartobeablipintestscorestwoyearspriortoevents.Asimilarblipisapparentforhigh-incomedistrictsinPanelB.Thereisnosignofsystematicpre-eventtrends.
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oftestscoreeffectstospendingeffectsislargeratthebottomoftheincome
distribution,consistentwiththeideathatfundingismoreproductiveinlow-income
districts,butequalratioscannotberuledout.
Table7presentsestimatesseparatelybygradeandsubject.Wecannotreject
thenullhypothesisofequaleffectsacrosseachdimension.
A. RobustnessTable8presentsestimatesofourkeyspecificationsfromourtwoalternative
approachestoeventmultiplicity.Column1repeatstheestimatesfromourpreferred
approachfromTables4and6.InColumn2,weincludeallidentifiedevents,creating
separatepanelsforeach;inColumn3,wefocusonlyonthefirstcourtorderineach
state.Resultsaresimilartothosefromourmainspecifications,thoughtheinitial
courtorderapproachyieldslessprecise,insignificantestimatesoffinanceeffects.
Onepotentialexplanationfortheachievementimpactsthatweidentifyis
thattheyreflectchangesinpopulationstratificationratherthanchangesin
educationalproduction.SFRsthatflattenthegradientofschoolfundingwithrespect
todistrictincomeandthatreducethelocalshareofschoolfinancereducethevalue
oflivinginahigh-incomedistrict,andmayleadsomehigh-incomefamiliesto
relocatetopreviouslylow-incomedistricts.Thiscouldleadtorisingachievementin
thesedistrictswithnochangeinschooleffectiveness.
Weassessthispossibilityinthreeways.First,wehavetestedwhether
between-districtincomegapsnarrowintheyearsfollowingSFRs.Wehavefoundno
evidenceforthis–districtlogincomesin2011arehighlycorrelatedwiththosein
1990,andthereisnosignthatgapsnarrowinstatesthathadreformsvs.thosethat
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29
didn’t.Second,wehaveconductedeventstudyanalyses,paralleltothosefortest
scores,fordistrictincomeorthedistrictnon-whiteorfree-orreduced-pricelunch
eligibleshare(AppendixTableA5).Inonlyonespecification–forthebetween-
quintilegapinthefreelunchshare–dowefindevidencethatthedemographic
compositionof(initially)low-incomedistrictschangesfollowingSFRs.Thisresultis
notrobust,andissmallrelativetothetestscoreimpactsthatweestimate.
Third,wedecomposetestscoresintotwocomponents,andestimate
separateSFReffectsoneach.Specifically,weestimateanindividual-levelregression
oftestscoresonstudentdemographiccharacteristics,poolingNAEPdataacross
yearsforeachgrade-subjectpairandincludingyearfixedeffects.Wethenconstruct
separateachievement-logdistrictincomegradientsfromthefittedvalues(excluding
thefixedeffects)forthisregression,representingstudentcharacteristicsthatwould
beaffectedbySFRsonlythroughchangesinsorting,andfromtheresiduals.Table9
presentsresultsofoureventstudyanalysesofthesegradients.Wepresenttwo
decompositions:Thefirstpanelusesonlyraceandgender,whichareconsistently
availableineachNAEPwave,alongwithschoolmeansofthese.Thenextuses
additionalcovariates,parentaleducationandfreelunchstatus,thatareless
consistentlyavailable,includingindicatorsforyearsinwhicheachisunavailable.
Thefirstsetofvariablesexplains22%ofthevarianceinstudenttestscores(netof
thesubject-grade-yeareffects),whilethesecondsetexplains28%.
Wefindnoevidencethatreformsaffectthedemographiccomponentofour
testscoreprogressivitymeasures.Pointestimatesarelessthanhalfthesizeofour
overalltestscoreimpacts,andareneversignificantlydifferentfromzero.By
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30
contrast,estimatedeffectsontheresidualcomponentoftestscoresareall
significant,andabouttwo-thirdsthesizeoftheoverallimpacts.Thus,whilewe
cannotruleoutsmalleffectsofSFRsonstudentsorting,therobustnessofeffectson
theresidualcomponentsupportsourinterpretationthatourresultsprimarily
reflectchangesineducationalproductioninlow-incomeschooldistricts.
Asafinalrobustnessexercise,wehavetestedwhethertheSFReffecton
achievementissensitivetoincludingcontrolsforthepresenceofaschool
accountabilitypolicyinastate,orwhethertheSFReffectvarieswithschool
accountability.Wefoundevidenceforneither.
VI. Financereformsandstatewideachievementgaps
Thefinaltopicthatweinvestigateiswhetherfinancereformsclosedoverall
testscoregapsbetweenhigh-andlow-achieving,minorityandwhite,orlow-income
andnon-low-incomestudentsinastate.Theseareperhapsbettermeasuresthan
ourslopesandquintilegapsoftheoveralleffectivenessofastate’seducational
systematdeliveringequitable,adequateservicestodisadvantagedstudents
(KruegerandWhitmore2002;CardandKrueger1992b).However,becausemost
inequalityiswithindistricts,changesinthedistributionofresourcesacrossdistricts
maynotbewellenoughtargetedtomeaningfullyclosethesegaps.
Table10presentsestimatesofeffectsonmeantestscoresacrossdifferent
subgroupsofinterest.Thefirstpanelshowsasmallandinsignificanteffectonmean
(pooled)testscores.Thisissomewhatofapuzzle,giventheincreasesinmean
revenuesdocumentedearlier.Itmustbenoted,however,thatourresearchdesignis
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31
morecredibleforoutcomedisparitiesthanforthelevelofoutcomes,asthelatter
wouldbeconfoundedbyunobservedshockstoaverageoutcomesinastatethatare
correlatedwiththetimingofschoolfinancereforms(Hanushek,Rivkin,andTaylor
1996a,b).Forexample,ifSFRsfollownegativeshockstomeanstudentachievement,
thiseffectwouldbedownward-biased.Anotherinterpretationisthatthemarginal
productivityofrevenuesisinfacthigherinlow-incomedistricts.
Thesecondpanelshowsimpactsonthestandarddeviationorinterquartile
rangeofachievementwithinstates,whilethethirdandfourthpanelspresent
resultsbyraceandincome,respectively.Thereisnodiscernibleeffecton
achievementgapsbyraceorincomeorontheoveralldispersionoftestscores.Point
estimatesareallroughlyafullorderofmagnitudesmallerthantheearlierestimates
fordistrict-levelprogressivityofmeanscores.
AppendixTablesA6andA7resolvethediscrepancy.Whilenon-whiteand
low-incomestudentsaremorelikelythantheirwhiteandhigher-incomepeersto
attendschoolinlow-incomeschooldistricts,thedifferencesarenotverylarge.
Roughlyone-quarterofnon-whitestudents,andone-thirdoflow-incomestudents,
liveinfirst-quintiledistricts,whileonly10%ofeachliveinfifth-quintiledistricts.
ThisleaveslittleroomforSFRstomuchaffecttherelativeresourcestowhichthe
typicalminority,low-income,orlowscoringstudentisexposed.
Toassessthismorecarefully,weassignedeachstudentthemeanrevenues
forhis/herdistrictandestimatedeventstudymodelsfortheblack-whiteorincome
gapintheseimputedrevenues.Results,inAppendixTableA7,indicatethatfinance
eventsraiserelativeper-pupilrevenuesintheaverageblackstudent’sschool
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districtbyonly$144(S.E.167),andreducerevenuesintheaveragelow-income
student’sdistrictby$23(S.E.262).Eveniffundingwasmuchmoreproductivethan
theaverageeffectimpliedbyouranalysis,thefundingchangesseenherewouldstill
notbeenoughtoyieldeffectsonblackorlow-incomestudents’averagetestscores
largeenoughtodetectwithourresearchdesign.Thus,whilereformsaimedatlow-
incomedistrictsappeartohavebeensuccessfulatraisingresourcesandoutcomes
inthesedistricts,weconcludethatwithin-districtchangeswouldbenecessaryto
havedramaticimpactsontheaveragelow-income,minority,orlow-scoringstudent.
VII. Discussion
Afterdesegregation,schoolfinancereformisperhapsthemostimportant
educationpolicychangeintheUnitedStatesinthelasthalfcentury.Butwhilethe
effectsofthefirst-andsecond-wavereformsonschoolfinancehavebeenwell
studied,thereislittleevidenceaboutthefinanceeffectsof“adequacy”reformsor
abouttheeffectsofanyofthesereformsonstudentachievement.Ourstudy
presentsnewevidenceoneachofthesequestions.
Wefindthatstate-levelschoolfinancereformsenactedduringtheadequacy
eramarkedlyincreasedtheprogressivityofschoolspending.Theydidnot
accomplishthisby"levelingdown"schoolfunding,butratherbyincreasing
spendingacrosstheboard,withlargerincreasesinlow-incomedistricts.Using
nationallyrepresentativedataonstudentachievement,wefindthatthisspending
wasproductive:Reformsincreasedtheabsoluteandrelativeachievementof
studentsinlow-incomedistricts.OurestimatesthuscomplementthoseofJacksonet
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33
al.(2016),whoexaminethelong-runimpactsofearlierschoolfinancereformsand
findsubstantialpositiveimpactsonavarietyoflong-runoutcomes.
Thedifferenttimepatternsofimpactsonresourcesandonstudent
outcomes,combinedwiththecumulativenatureofthelatter,preventsasimple
instrumentalvariablesinterpretationofthereduced-formcoefficientsintermsof
theachievementeffectperdollarspent–itisnotclearwhichyears’revenuesare
relevanttotheaccumulatedachievementofstudentstestedryearsafteranevent.
Toassessthemagnitudeoftheimpactsweestimate,wefocusonestimatedeffects
onstudentachievementtenyearsafteranevent.Becauseeffectsonschool
resourcesarestableintheyearsfollowingevents,thesecanbeinterpretedasthe
impactofachangeinresourcesforeveryyearofastudent’scareer(through8th
grade).Nevertheless,thefocusonther=10estimateisarbitrary.Wewouldobtain
largerestimatesoftheachievementeffectperdollarifweusedimpactsmorethan
tenyearsafterevents,orsmallereffectswithashorterwindow.
Ourpreferredestimates,basedonthegradientofstudentachievementwith
respecttodistrictincome,indicatethatanSFRraisesachievementinadistrictwith
logaverageincomeonepointbelowthestatemean,relativetoadistrictatthe
mean,by0.1standarddeviationsaftertenyears.Ourfinanceestimatesindicatethat
thisdistrictsawanincreaseinrelativestateaidof$622perpupilforeachofthose
tenyears,andanincreaseintotalrevenuesof$424perpupil.
$424perpupilinspendingeachyearfromkindergartenthroughgrade8,
discountedtothestudent’skindergartenyearusinga3%rate,correspondstoa
presentdiscountedcostof$3,400.Chettyetal.(2011)estimatethata0.1standard
-
34
deviationincreaseinkindergartentestscorestranslatesintoincreasedearningsin
adulthoodwithpresentvalueof$5,350perpupil.Thisimpliesabenefit-costratioof
1.5,evenwhenonlyearningsimpactsarecountedasbenefits.28
Thisratioisnotwhollyrobust.Ourquintileanalysisshowslargerrevenue
effects,implyingabenefit-costratiobelowone,whileJacksonetal.’s(2016)studyof
theeffectsofearlierfinancereformsonstudents’adultoutcomesimpliesmuch
largerbenefitsperdollarthandoesourcalculation.Thus,althoughthesesortsof
calculationsarequiteimprecise,theevidenceappearstoindicatethatthespending
enabledbyfinancereformswascost-effective,evenwithoutaccountingfor
beneficialdistributionaleffects.
Itisimportanttonotethatourresearchdesignispoorlysuitedtoidentifying
theoptimalallocationofschoolresourcesacrossexpenditurecategories,orto
testingwhetheractualallocationsareclosetooptimal.Itallowsusonlytosaythat
theaveragefinancereform—whichweinterprettoinvolveroughlyunconstrained
increasesinresources,thoughinsomecasestheadditionalfundswereearmarked
forparticularprogramsortiedtootherreforms—ledtoaproductive(though
perhapsnotmaximallyproductive)useofthefunds.29
Ourresultsthusshowthatmoneycananddoesmatterineducation,and
complementsimilarresultsforthelong-runimpactsofschoolfinancereformsfrom
Jacksonetal.(2016).Schoolfinancereformsareblunttools,andsomecritics
28Theearningseffectsofincreasesin8thgradetestscoresarelikelylargerthanthoseofincreasesinKindergartenscores,sousingestimatesofthelatterbiasesourbenefitcalculationdownward.29Strongerschoolaccountabilitymayprovideincentivestoschoolstoallocatetheirresourcesmoreefficiently(Hanushek2006).Weinvestigatedspecificationsthatallowedforinteractionsbetweenfinancereformeventsandthestate’saccountabilitypolicy,butfoundnoevidenceforthis.
-
35
(Hanushek,2006;Hoxby,2001)havearguedthattheywillbeoffsetbychangesin
districtorvoterchoicesovertaxratesorthatfundswillbespentsoinefficientlyas
tobewasted.Ourresultsdonotsupporttheseclaims.Courtsandlegislaturescan
evidentlyforceimprovementsinschoolqualityforstudentsinlow-incomedistricts.
Butthereisanimportantcaveattothisconclusion.AswediscussinSection
VI,theaveragelow-incomestudentdoesnotliveinaparticularlylow-income
district,soisnotwelltargetedbyatransferofresourcestothelatter.Thus,wefind
thatfinancereformsreducedachievementgapsbetweenhigh-andlow-income
schooldistrictsbutdidnothavedetectableeffectsonresourceorachievementgaps
betweenhigh-andlow-income(orwhiteandblack)students.Attackingthesegaps
viaschoolfinancepolicieswouldrequirechangingtheallocationofresourceswithin
schooldistricts,somethingthatwasnotattemptedbythereformsthatwestudy.
-
36
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-
Figures
Figure 1: Mean revenues per pupil for highest and lowest income school districts, 1990-2012
80
00
10
00
01
20
00
14
00
0Q
1,
Q5
Me
an
To
tal R
eve
nu
es
1990 1995 2000 2005 2010Year
Q1 Mean Q5 Mean
Notes: Highest (lowest) income districts are those in the top (bottom) 20% of their states’ district-leveldistributions of mean household income in 1990, and are labeled as ”Q5” and ”Q1”, respectively. Seeappendix for details of quintile classifications. Revenues are expressed in real 2013 dollars. Districts areaveraged within states, weighing by log district enrollment; states are then averaged without weights. Hawaiiand the District of Columbia are excluded.
39
-
Figure 2: Gap in revenues per pupil between lowest and highest income districts, by state finance reformstatus, 1990-2012
−1
00
0−
50
00
50
01
00
0
Q1
−Q
5 M
ea
n T
ota
l R
eve
nu
es
1990 1995 2000 2005 2010
Year
No Reform States Finance Reform States
Notes: See notes to Figure 1. Finance reform states are those with school finance reforms between 1990 and2011, as listed in Appendix Table A1. Lines show unweighted best linear fit to time series.
40
-
Figure 3: Gap in average test scores between lowest and highest income districts, by state finance reformstatus, 1990-2011
−.7
−.6
−.5
−.4
Q1
−Q
5 M
ea
n S
co
re
1990 1995 2000 2005 2010
Year
No Reform States Finance Reform States
Notes: Lowest (Q1) and highest (Q5) income districts are defined as in Figure 1. NAEP observations indistricts in each quintile are averaged, using NAEP sampling weights and separately for each grade andsubject tested, and the Q1-Q5 di↵erence is computed for each state. State-grade-subject Q1-Q5 di↵erencesare averaged separately for each group of states, weighting by the harmonic mean of the sum of the studentweights in Q1 and Q5 districts. Lines show best linear fit to the time series.
41
-
Figure 4: Timing of school finance events
02
46
8E
ven
ts p
er
yea
r
1990 2000 2010Year
Statute
Court
Notes: Each entry represents a state with a school finance reform event (a major court ruling and/orsubstantial statutory change) in a particular year. States may have multiple events. When states havemultiple events in the same year, they are counted only once, as a court event if any of the events were courtrulings and as a statute otherwise. Events are listed in Appendix Table A1.
42
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Figure 5: Geographic distribution of post-1989 school finance events
No Event
Post-1990 Reform Event
Notes: Map indicates states that had school finance reform events, as listed in Appendix Table A1, between1990 and 2011.
43
-
Figure 6: State revenues per pupil vs. district income, Ohio, 1990 and 2012
05000
10000
15000
20000
9.5 10 10.5 11 11.5 12
1990
05000
10000
15000
20000
9.5 10 10.5 11 11.5 12
2012
Sta
te a
id p
er
pupil
(2013$)
ln(district avg. HH income, 1990)
Notes: Each circle represents one district; size is proportional to average district enrollment over 1990-2012.Solid lines represent a regression of state revenue per pupil (2013$) on log 1990 district mean householdincome, controlling for enrollment and district type (see footnote 16). Dashed lines represent means amongdistricts in each quintile of the district mean income distribution.
44
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Figure 7: Progressivity of state revenue distributions, Ohio, 1990-2012
10
00
20
00
30
00
40
00
50
00
20
13
$ p
er
pu
pil
1990 1995 2000 2005 2010Fiscal year
Q1−Q5 difference
−1*(Log income gradients)
Notes: Dark line represents the di↵erence in mean state revenue per pupil (2013$) between the lowest (Q1)and highest (Q5) income districts in Ohio. Districts are classified based on 1990 mean household incomeand are weighted by log enrollment; see notes to Figure 1 for details. Lighter line represents regressions ofstate revenue per pupil on log mean income, controlling for enrollment and district type (see footnote 16); inthis figure, coe�cients are multiplied by -1 to facilitate comparisons. Solid vertical lines represent plainti↵victories in the Ohio Supreme Court in De Rolph v State I, II, and IV in 1997, 2000, and 2002.
45
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Figure 8: Event study estimates of e↵ects of school finance reforms on mean state and total revenues
−2000
−1000
01000
2000
Change in
mean s
tate
reve
nues
−5 0 5 10 15 20Years Since Event
Non−Parametric Estimate Parametric Estimate
(a) State revenue
−2000
−1000
01000
2000
Change in
mean tota
l reve
nues
−5 0 5 10 15 20Years Since Event
Non−Parametric Estimate Parametric Estimate
(b) Total revenue
Notes: Figure displays coe�cients from event study regressions, where the dependent variable is mean state(panel A) and total (panel B) revenues per pupil (2013$) across all districts in a state. Dashed lines showthe three-parameter parametric model (equation 2). Solid lines show the non-parametric model (equation3), with the event year (indicated as 0) as the excluded category; dotted lines represent 95% confidenceintervals. Estimates for the parametric models are reported in Table 3, Panel A, Columns 2 and 4. p valuesfor omnibus hypothesis tests of zero pre- and post-event e↵ects in the non-parametric model are 0.31 and¡0.001, respectively, in Panel A, and 0.15 and ¡0.001 in Panel B. In the parametric model, the p-value forthe hypothesis that the pre-event trend is zero is 0.18 in Panel A and 0.79 in Panel B; for the test that thepost-event jump and change in trend is zero it is 0.11 and 0.01, respectively.
46
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Figure 9: Event study estimates of e↵ects of school finance reforms on mean revenues in lowest and highestincome districts
−2000
−1000
01000
2000
Change in
Q1 m
ean s
tate
reve
nues
−5 0 5 10 15 20Years Since Event
Non−Parametric Estimate Parametric Estimate
(a) State revenue, Q1−
2000
−1000
01000
2000
Change in
Q1 m
ean tota
l reve
nues
−5 0 5 10 15 20Years Since Event
Non−Parametric Estimate Parametric Estimate
(b) Total revenue, Q1
−2000
−1000
01000
2000
Change in
Q5 m
ean s
tate
reve
nues
−5 0 5 10 15 20Years Since Event
Non−Parametric Estimate Parametric Estimate
(c) State revenue, Q5
−2000
−1000
01000
2000
Change in
Q5 m
ean tota
l reve
nues
−5 0 5 10 15 20Years Since Event
Non−Parametric Estimate Parametric Estimate
(d) Total revenue, Q5
Notes: Figure displays coe�cients from event study regressions. Dependent variables are mean state revenuesin the lowest income quintile of districts (panel A), mean total revenues in these districts (panel B), andmean state and total revenues in the highest income quintile of districts (panels C and D, respectively), allmeasured in 2013 dollars per pupil. Dashed lines show the three-parameter parametric model (equation 2).Solid lines shows the non-parametric model (equation 3), with the event year (indicated as 0) as the excludedcategory; dotted lines represent 95% confidence intervals. Estimates for the parametric models are reportedin Table 3, Panels B and C, Columns 2 and 4. p values for omnibus hypothesis tests of zero post-evente↵ects in the non-parametric model in Panels A-D are 0.53, 0.39, 0.41, and 0.74, respectively; p-values forzero pre-event e↵ects are ¡0.001 in all panels. In the parametric model, the p-values for the hypothesis thatthe pre-event trend is zero are 0.24, 0.68, 0.21, and 0.78; for the test that the post-event jump and changein trend is zero they are 0.01, ¡0.001, 0.30, and 0.22.
47
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Figure 10: Event study estimates of e↵ects of school finance reforms on progressivity of district revenues
−2000
−1000
01000
2000
Change in
Q1−
Q5 m
ean tota
l reve
nues
−5 0 5 10 15 20Years Since Event
Non−Parametric Estimate Parametric Estimate
(a) Q1-Q5 mean
−2000
−1000
01000
Change in
tota
l reve
nue s
lope
−5 0 5 10 15 20Years Since Event
Non−Parametric Estimate Parametric Estimate
(b) Total revenue slope
Notes: Figure displays coe�cients from event study regressions. Dependent variables are the di↵erence inmean total revenues per pupil (in 2013$) between districts in the bottom and top quintile by mean familyincome in the state (panel A), and the slope of total per-pupil revenues (in 2013$) with respect to logmean family income, controlling for log enrollment and district type (panel B). Dashed lines show the three-parameter parametric model (equation 2). Solid lines shows the non-parametric model (equation 3), withthe event year (indicated as 0) as the excluded category; dotted lines represent 95% confidence intervals.Estimates for the parametric models are reported in Table 4, Panels A and B, Columns 2 and 4. p-valuesfor omnibus hypothesis tests of zero pre-event e↵ects in the non-parametric model are 0.86 in Panel A and0.96 in Panel B; p-values for zero post-event e↵ects are ¡0.001 in each panel. In the parametric model, thep-value for the hypothesis that the pre-event trend is zero is 0.72 in Panel A and 0.58 in Panel B; for thetest that the post-event jump and change in trend is zero it is 0.01 and 0.11, respectively.
48
-
Figure 11: Event study estimates of e↵ects of school finance reforms on progressivity of test scores
−.3
−.2
−.1
0.1
Ch
an
ge
in t
est
sco
re s
lop
e
−5 0 5 10 15 20Years Since Event
Non−Parametric Estimate Parametric Estimate
Notes: Figure displays coe�cients from event study regressions. Dependent variable is the slope of meantest scores with respect to log mean family income, controlling for log enrollment. Dashed lines show thethree-parameter parametric model (equation 2). Solid lines shows the non-parametric model (equation 3),with the event year (indicated as 0) as the excluded category; dotted lines represent 95% confidence intervals.Both event study regressions include state and subject-grade-year fixed e↵ects. Estimates for the parametricmodels are reported in Table 6, Column 1. p-values for the hypothesis that pre-event e↵ects are zero are 0.43in the non-parametric model and 0.80 in the parametric model; for zero post-event e↵ects, they are ¡0.001and 0.02, respectively.
49
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Figure 12: Event study estimates of e↵ects of school finance reforms on mean test scores in highest andlowest income school districts
−.1
0.1
.2.3
Change in
Q1 M
ean T
est
Sco
res
−5 0 5 10 15 20Years Since Event
Non−Parametric Estimate Parametric Estimate
(a) Q1 mean test scores
−.1
0.1
.2.3
Change in
Q5 M
ean T
est
Sco
res
−5 0 5 10 15 20Years Since Event
Non−Parametric Estimate Parametric Estimate
(b) Q5 mean test scores
Notes: Figure displays coe�cients from event study regressions. Dependent variables are mean test scores forstudents at districts in the bottom quintile (panel A) or top quintile (panel B) of the state’s distribution of1990 district mean household incomes. Dashed lines show the three-parameter parametric model (equation2). Solid lines shows the non-parametric model (equation 3), with the event year (indicated as 0) as theexcluded category; dotted lines represent 95% confidence intervals. Both event study regressions includestate and subject-grade-year fixed e↵ects. p-values for omnibus hypothesis tests of zero pre-event e↵ects inthe non-parametric model are 0.01 in Panel A and 0.02 in Panel B; p-values for zero post-event e↵ects are¡0.001 in each panel. In the parametric model, the p-value for the hypothesis that the pre-event trend is zerois 0.59 in Panel A and 0.10 in Panel B; for the test that the post-event jump and change in trend is zero itis 0.01 and 0.34, respectively.
50
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Tables
Table 1: NAEP Testing Years
Year Subjects and grades covered Number of Number ofMath G4 Math G8 Reading G4 Reading G8 States Students
1990 X 38 97,9001992 X X X 42 321,1201994 X 41 104,8901996 X X 45 228,9801998 X X 41 206,8102000 X X 42 201,1102002 X X 51 270,2302003 X X X X 51 691,3602005 X X X X 51 674,4202007 X X X X 51 711,3602009 X X X X 51 775,0602011 X X X X 51 749,250
Notes: In final column, students are cumulated across all tested subjects and grades, and rounded to thenearest 10.
51
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Table 2: Summary statistics
(a) District-year panel
Overall Mean by subgroup
N Mean SD Q1 Q5
Enrollment 229,386 67,523 181,811 13,738 30,019
Log(mean income, 1990) 223,334 10.53 .2935 10.21 10.9
Total revenue p.p. 229,386 11,087 3,489 10,803 11,884
State 229,386 5,135 2,291 6,373 4,007
Local 229,386 5,094 3,273 3,257 7,359
Federal 229,386 858.2 641.4 1,173 519.1
Expenditures p.p. 229,386 11,264 3,685 10,831 12,125
Instructional 229,386 5,845 1,953 5,661 6,180
Non-instructional 229,386 5,419 2,221 5,169 5,944
NAEP scores 49,867 .2559 .4578 .02941 .5887
(b) State-year panel
N Q1 Q5 Q1-Q5 di↵erence Gradient
Mean SD Mean SD Mean SD Mean SD
Log(mean income, 1990) 49 10.2 .135 10.8 .234 -.645 .167
Total revenue p.p. 1,078 11,527 3,905 11,844 3,351 -329 2,158 539 3,574
State 1,078 6,552 2,822 4,347 2,006 2,196 2,244 -3,086 3,470
Local 1,078 3,658 1,600 6,893 3,477 -3,231 2,624 5,190 3,313
Federal 1,078 1,317 1,082 604 482 706 722 -1,565 1,532
Mean NAEP score 532 .0372 .316 .511 .303 -.474 .318 .955 .337
Notes: Panel (a) reports summary statistics at the district by year level, weighted by district enrollmentfor the financial variables and by the sum of the student weights for the mean NAEP score. Panel (b) showssummary statistics for the unweighted state-year panel.
52
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Table 3: Event study estimates of e↵ects of school finance reforms on mean revenues per pupil, by districtincome
State Revenue Total Revenue
1p 3p 1p 3p
Mean:
Post Event 912⇤⇤ 672⇤⇤ 829⇤⇤⇤ 839⇤⇤⇤
(359) (320) (302) (269)Trend 68 9
(50) (32)Post Event * Yrs Elapsed -61 -17
(60) (52)
Observations 1,078 1,078 1,078 1,078
Q1 Mean:
Post Event 1,225⇤⇤⇤ 954⇤⇤⇤ 1,233⇤⇤⇤ 1,164⇤⇤⇤
(343) (302) (370) (287)Trend 60 16
(50) (39)Post Event * Yrs Elapsed -40 -11
(70) (70)
Observations 1,078 1,078 1,078 1,078
Q5 Mean:
Post Event 527 351 544⇤⇤ 471⇤
(378) (325) (277) (277)Trend 72 9
(56) (32)Post Event * Yrs Elapsed -84 2
(61) (41)
Observations 1,076 1,076 1,076 1,076
Notes: Table reports estimates of the parametric event study models, equations (1) (columns 1 and3) and (2) (columns 2 and 4). Dependent variables are mean state revenues per pupil (columns 1-2) andmean total revenues per pupil (columns 3-4), weighting districts by their log enrollment; each is computedseparately for each state and year. In panel A, means are computed over all districts in each state; in panelsB and C, they are computed over the bottom and top, respectively, quintiles of the states’ district 1990mean household income distributions. Event study regressions include state and year fixed e↵ects, and areunweighted. Standard errors clustered at the state level.
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Table 4: Event study estimates of e↵ects of school finance reforms on progressivity of school finance
State Revenue Total Revenue
1p 3p 1p 3p
Q1-Q5 Mean:
Post Event 711⇤⇤ 606⇤⇤⇤ 701⇤⇤ 696⇤⇤⇤
(316) (231) (309) (243)Trend -10 9
(25) (24)Post Event * Yrs Elapsed 42 -14
(36) (44)
Observations 1,076 1,076 1,076 1,076
Slopes:
Post Event -622⇤⇤⇤ -522⇤⇤ -424 -469⇤⇤
(223) (209) (304) (233)Trend -11 -25
(25) (45)Post Event * Yrs Elapsed -5 53
(21) (61)
Observations 1,078 1,078 1,078 1,078
Notes: Table reports estimates of the parametric event study models, equations (1) (columns 1 and3) and (2) (columns 2 and 4). In Panel A, dependent variable is the gap in state (columns 1-2) or total(columns 3-4) revenues per pupil between districts in the bottom and top quintiles of the states’ district 1990mean household income distributions. In Panel B, dependent variable is the coe�cient from a district-levelregression of the relevant per-pupil revenue measure on the log of the district’s 1990 mean household income,controlling for district log enrollment and district type (elementary / secondary / unified) and weighting bythe district’s average log enrollment over time. Event study regressions include state and year fixed e↵ects.Event study regressions are unweighted in Panel A, and is weighted by the inverse squared standard errorof the dependent variable in Panel B. Standard errors clustered at the state level.
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Table 5: Event study estimates of e↵ects of school finance reforms on components of district finance
Mean of depvar Mean Q1 Mean Q1-Q5 Mean Slope
Revenue E↵ects:
Total revenue 11,593 829⇤⇤⇤ 1,233⇤⇤⇤ 701⇤⇤ -424(302) (370) (309) (304)
State revenue 5,449 912⇤⇤ 1,225⇤⇤⇤ 711⇤⇤ -622⇤⇤⇤
(359) (343) (316) (223)Local revenue 5,238 -146 -126 -126 90
(307) (233) (235) (339)Federal revenue 907 63 134 116 34
(83) (143) (116) (33)
Expenditure E↵ects:
Total expenditures 11,595 907⇤⇤⇤ 1,377⇤⇤⇤ 753⇤⇤ -449(290) (367) (309) (309)
Current instructional exp. 6,000 443⇤⇤⇤ 604⇤⇤⇤ 243⇤ -161(134) (155) (127) (208)
Teacher salaries + benefits 5,533 339⇤⇤ 449⇤⇤⇤ 143 -103(153) (169) (117) (189)
Mean teacher salary 63,425 -286 -245 272 -259(1,024) (1,107) (947) (1,122)
Pupil teacher ratio 15.40 -0.60⇤⇤⇤ -0.66⇤⇤⇤ 0.01 0.23(0.19) (0.19) (0.20) (0.17)
Non-instructional exp 5,595 464⇤⇤ 773⇤⇤⇤ 511⇤⇤ -232(186) (257) (235) (176)
Student support 3,426 221⇤⇤ 299⇤⇤ 100 -81(102) (119) (83) (88)
Total capital outlays 1,076 272⇤⇤ 486⇤⇤⇤ 369⇤⇤ -87(114) (177) (181) (78)
Other current exp. 431.0 7.9 9.2 -2.5 -2.9(12.4) (14.5) (13.3) (12.1)
Notes: Each entry in columns 2-5 represents the coe�cient from a separate event study regression, usingthe one-parameter specification in equation (1). Dependent variables are constructed from district-levelfinance summaries indicated by row headings and expressed in per-pupil terms; means across districts arereported in column 1. Specifications correspond to columns 1 and 2 of Table 3, panels A (column 2) and B(column 3), and Table 4, panels A (column 4) and B (column 5). See notes to Tables 3 and 4.
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Table 6: Event study estimates of e↵ects of school finance reforms on student achievement
Slopes Q1 Q5 Q1-Q5
(1) (2) (3) (4) (5) (6)
Post Event * Yrs Elapsed -0.011⇤⇤ -0.010⇤⇤⇤ 0.007⇤⇤ -0.001 0.008⇤⇤ 0.014⇤⇤
(0.004) (0.003) (0.003) (0.004) (0.004) (0.005)
Trend 0.001 -0.007(0.003) (0.005)
Post Event 0.001 0.011(0.023) (0.024)
Observations 1498 1498 1509 1507 1505 1505p, total event e↵ect=0 0.02 0.01 0.01 0.84 0.05 0.04State FEs X X X X X XSub-gr-yr FEs X X X X X X
Notes: Each column represents a separate event study regression, using specification (2) and, in columns2-5, constraining �jump = �trend = 0. Dependent variable in columns 1-2 is the slope of test scores with re-spect to log mean 1990 income in the district, using NAEP weights and controlling for log district enrollment.In columns 3-4, dependent variable is the weighted mean score in districts in the bottom or top quintile,respectively, of the state district-level income distribution. In columns 5-6, dependent variable is the di↵er-ence between the bottom and top quintiles. All are computed separately for each state-year-subject-gradecell with available data. All event study specifications include state and subject-grade-year fixed e↵ects, andare weighted by the inverse squared standard error of the dependent variable. p-values for total event e↵ectin columns 1 and 6 test the hypothesis that the �jump and �phasein coe�cients are both zero; in columns2-5, the p-value is for the hypothesis that �phasein = 0, with �jump constrained to zero.
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Table 7: Event study estimates of e↵ects of school finance reforms on student achievement by subject andgrade
Test Score Slope Q1-Q5 Mean
Pooled -0.010⇤⇤⇤ 0.008⇤⇤
(0.003) (0.004)
By Subject :
Math -0.012⇤⇤⇤ 0.007⇤
(0.003) (0.004)Reading -0.006 0.008⇤
(0.005) (0.004)
Di↵erence -0.006 -0.001p-value 0.09 0.68
By Grade:
G4 -0.010⇤⇤ 0.008(0.005) (0.005)
G8 -0.010⇤⇤ 0.008⇤⇤
(0.004) (0.004)
Di↵erence 0.000 -0.000p-value 0.93 0.96
Notes: First row repeats specifications from Table 6, columns 2 and 5. See notes to that table for details.Subsequent models restrict the event study sample to slope and quintile gaps computed in specific subjectsor grades. Di↵erence entries report the di↵erence in coe�cients between math and reading or grade 4 andgrade 8 specifications, with p-values for the hypothesis that the event study coe�cient is equal in the twosubsamples.
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Table 8: Sensitivity of event study estimates to the treatment of states with multiple events
Selected Events All events (stacked) Initial court events
Panel A: Gradients
State revenue p.p. -622⇤⇤⇤ -479⇤⇤⇤ -432⇤
(223) (160) (222)Total revenue p.p. -424 -197 -399
(304) (269) (292)NAEP scores -0.010⇤⇤⇤ -0.009⇤⇤⇤ -0.009⇤⇤⇤