SchoolFinanceReformandtheDistributionofStudentAchievement*

July2016

JulienLafortune

UniversityofCalifornia,Berkeleyjulien@econ.berkeley.edu

JesseRothstein

UniversityofCalifornia,BerkeleyandNBER

rothstein@berkeley.edu

DianeWhitmoreSchanzenbachNorthwesternUniversity

andNBERdws@northwestern.edu

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

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.

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.

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.

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.

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

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

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.

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.

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

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.

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.

28

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

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

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

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

32

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

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

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

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

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

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

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

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

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

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

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.

53

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⇤⇤⇤