University of Groningen
The ant or the grasshopper? The long-term consequences of Unilateral Divorce Laws on
savings of European households
Angelini, Viola; Bertoni, Marco; Stella, L.; Weiss, C.
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European Economic Review
DOI:
10.1016/j.euroecorev.2019.07.002
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Angelini, V., Bertoni, M., Stella, L., & Weiss, C. (2019). The ant or the grasshopper? The long-term
consequences of Unilateral Divorce Laws on savings of European households. European Economic
Review, 119, 97-113. https://doi.org/10.1016/j.euroecorev.2019.07.002
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ContentslistsavailableatScienceDirect
European
Economic
Review
journalhomepage:www.elsevier.com/locate/euroecorev
The
ant
or
the
grasshopper?
The
long-term
consequences
of
Unilateral
Divorce
Laws
on
savings
of
European
households
Viola
Angelini
a,
Marco
Bertoni
b,∗,
Luca
Stella
c,
Christoph T.
Weiss
da University of Groningen and Netspar, the Netherlands
b Department of Economics and Management “Marco Fanno”, University of Padova, Via del Santo 33, Padova 35123, Italy; HEDG and IZA,
Italy
c Bocconi University and IZA, Italy d European Investment Bank, Luxembourg
a
r
t
i
c
l
e
i
n
f
o
Article history: Received 27 July 2018 Accepted 1 July 2019 Available online 12 July 2019
JEL classification: G11 J12 J22 J32 Keywords: Divorce risk Household savings Europe
a
b
s
t
r
a
c
t
UnilateralDivorceLaws(UDLs)allowpeopletoobtaindivorcewithouttheconsentoftheir spouse.UsingthestaggeredintroductionofUDLsacrossEuropeancountries,weshowthat householdsexposedtoUDLsforalongerperiodoftimeaccumulate moresavings.This effectholdsforbothfinancialandtotalwealthandisstrongerathigherquantilesofthe wealthdistribution.Consistentwithaprecautionarymotiveforsavings,wealsofindthat exposuretoUDLsincreasesfemalelaboursupply,numeracy,trustinothers and disposi-tionaloptimism.
© 2019TheAuthor(s).PublishedbyElsevierB.V. ThisisanopenaccessarticleundertheCCBY-NC-NDlicense. (http://creativecommons.org/licenses/by-nc-nd/4.0/)
1. Introduction
Inthesecond halfofthetwentiethcentury,awaveofliberalreformstodivorcelawtook placeacrossmanydeveloped countries.Byallowingpeopletoobtaindivorcewithouttheconsentoftheirspouse,thenewly-introducedUnilateralDivorce Laws (UDLs) raised the risk of divorce andchanged the allocation of bargainingpower betweenpartners. The economic literaturehasinvestigatedtheshort-termeffectsoftheadoptionofUDLsonalargearrayofhouseholdoutcomes,including maritalconflict(StevensonandWolfers,2006;2007),well-beingofchildren(Gruber,2004;Reinholdetal.,2013),women’s laboursupplydecisions(Gray,1998;Stevenson,2007),andhouseholdsavingbehaviour(González andÖzcan,2013;Voena, 2015).
Froman economicperspective,thereare severalcompetingchannelsthrough whichUDLsmayaffectmarriage-specific investmentsandassetsaccumulation.CubedduandRios-Rull(1997)arguethattheincreaseddivorceriskinducedbyUDLs mayencouragehouseholds’savingbehaviourbyastandardprecautionarymotive:asdivorceiscostly(bothduetothelegal feesandbecause of theloss in economiesof scale andrisk-sharingopportunities) and householdscannot hedge against thisnegativeshockon themarket,ahigherriskofseparationinducesmarried couplestosavemore.Voena (2015)claims that,underaregimeofequaldivisionofpropertyupondivorce,UDLscanaffectsavingbehaviourthroughoutthemarriage
∗ Corresponding author at: University of Padova, HEDG and IZA, Italy.
E-mail address: marco.bertoni@unipd.it (M. Bertoni).
https://doi.org/10.1016/j.euroecorev.2019.07.002
0014-2921/© 2019 The Author(s). Published by Elsevier B.V. This is an open access article under the CC BY-NC-ND license. ( http://creativecommons.org/licenses/by-nc-nd/4.0/ )
period,byallowingpartnerstoexerciseacredibledivorcethreat.Thisshouldincreasethebargainingpowerofthemember ofthecouplewithalowershareinhouseholdresources– usuallythewife– withpositiveeffectsonsavings,ashusbands willsavemore toself-insure againsttheloss ofhalfoftheir wealthupondivorce. However,Mazzocco etal.(2014) stress that anincrease intheprobabilityofdivorce mayadversely affectsavingpropensitywhilemarried, asassetdivisionlaws impose a division of marital propertieswithin thecouple. In their model,this channel creates incentivesfor spouses to increasecurrentconsumptionanddecreasemarriage-specificinvestments.
Tothebestofourknowledge,onlyafewcontributionshaveattemptedtotestwhichofthesechannelsdominatesin prac-tice,andtheresultingempiricalevidenceremainsratherinconclusive. Forinstance,whileGonzález andÖzcan(2013) and
Pericoli and Ventura (2012) provide support for the precautionary saving channel, Stevenson (2007) reportsevidence of a decline in the propensity to undertake marriage-specific investments, such as buying a house orsupporting a spouse throughschool.Inaddition,littleattentionhasbeenpaidtothelonger-runeffectsofUDLsonthesavingsofcouplesaround retirement. Thisis somewhat surprising,giventhe increasing concerns thata large cohort ofbaby boomers is approach-ing retirementwithlittlesavings andvirtuallynoassetsother thantheirhome (Lusardi andMitchell, 2014).The problem isparticularly seriousforwomen, who tendto livelongerthan men, havelessattachmentto thelabourforce, earnless, contributelesstopensionplansandarelessfinanciallyliterate(LusardiandMitchell,2007;2008;Hsu,2016).
In thispaper, we explore thelong-term consequencesof exposure to UDLs on thewealth ofmarried couples around retirementageinEurope.Severalpapersalreadyprovideevidenceaboutthestarkincrease inmaritalseparationfollowing theintroductionofUDLs acrossEuropeancountries. Forinstance,González andViitanen(2009)findthattheintroduction of UDLs haspermanentlyincreased divorce ratesin Europeby about0.6annual divorcesper 1000people, a large effect consideringthattheEuropeanaverageannualdivorceratein2002was2per1000people.1
Our analysis uses cross-sectional and life-history data from the Survey of Health, Ageing and Retirement in Europe (SHARE). Our final sample consistsof close to 2700 couples whose head is between50 and 70years old, who are still in their first marriageat thetime ofthe SHARE interviewand reside in one ofthe seven European countriesthat have adopted UDLs inthesecond half ofthe twentiethcentury (Austria, Belgium, Denmark,France, Germany,theNetherlands andSpain).WiththeexceptionofAustriaandtheSpanishregionofCatalonia– whereseparationofpropertyupondivorce holds– equalsharingofpropertyupondivorceisthedefaultinthesecountries.2
Ourresearch design exploits the staggered timing ofthe introductionofUDLs acrossthesecountries toidentify their reduced-form effecton householdsavings. Since thedistribution of wealthis veryskewed, we rely on bothmedian and meanwealthregressions.Tounderstand theeffectofUDLson theentiredistributionofsavings, wealsousea setof un-conditional quantileregressions (seeFirpo etal., 2009).Ourempirical analysispaysspecialattentiontodeal withseveral threatstointernalvalidity, relatedtoselectionintoandoutsideofmarriageinducedbytheintroductionofUDLs,omitted variablesbias,concurringshocks,andanticipationeffects.
We findthat an additionalyearofexposure toUDLs increasesmedian netfinancial wealthby approximately6%.This effectisparticularlypronouncedamongmoreaffluenthouseholds:weestimate thattheeffectofUDLexposureiscloseto zeroatthefirstdecileofthewealthdistribution,andincreasesathigherpercentiles.Ourestimatesaresmallerinmagnitude andabitlessprecisewhenweusetotalwealth(i.e.,thesumofrealandfinancialassets)asanalternativemeasureofthe dependent variable.Thisfindingisconsistent withthe ideathat realassetsrepresentthewealthcomponentthatis most difficulttochange.
Inthesecond partofouranalysis,we exploitthebreadthofoursurveydatatobetterunderstandthepotential mecha-nismsthroughwhichexposuretoUDLsmayaffectsavings.Weshowthat exposuretoUDLsleadstohigherfemale labour supply, numeracy, trust in othersanddispositional optimism.Overall, these findings are consistent witha precautionary saving explanation,inwhich thewife self-insuresagainstthe risk ofnegativeshocksassociated withdivorce.Instead, an increaseinthebargainingpowerofthewomanseemslesslikelytobeanexplanationforourresultssincethiswouldimply adecreaseinfemalelaboursupply,asshownbyVoena(2015).
Ourcontributiontotheliteratureisthreefold.First,wefocusonthelong-termeffectsofexposuretoUDLsonthewhole distributionofhouseholds’financialandtotalwealtharoundtheretirementage.Thisdifferentiatesourworkfromprevious studiesthatestimate theshort-runimpactofUDLs onmeanhouseholdsavingoronthesavingrate(GonzálezandÖzcan, 2013;Voena, 2015).Second, by exploitingdataand quasi-experimentalvariation across countries, weare able toprovide causalestimatesthat arevalidforseveralEuropeancountries, therebyincreasing theexternal validityofourstudy.Third, therichnessofourdataallowsustodigdeeperintothemechanismsunderlyingtherelationshipbetweenexposuretoUDLs andhouseholdsavings.Overall,ourresultsprovidesupportfortheprecautionarymotiveforsaving.
Theremainderofthispaperisorganisedasfollows.Section2describesthedataandprovidesbackgroundinformationon UDLsreformsinEurope.Section3discussestheidentificationstrategyandempiricalmodel.Themainresultsofthepaper
1 This is in line with the evidence provided by Kneip et al. (2014) and Kneip and Bauer (2009) who estimate that the introduction of UDLs accounts for about one quarter of the total rise in divorce rates in Europe between 1960 and 20 0 0. Comparable evidence for the US is provided by Friedberg (1998) , who finds that UDLs have permanently raised divorce rates by 0.4 divorces per 10 0 0 people, accounting for almost 20% of the increase in divorce rates between 1968 and 1988 in the US. However, using data for a longer time span and accounting for dynamic effects, Wolf ers (2006) shows that the actual increase in the US is lower, at only 0.2 to 0.3 divorces per 10 0 0 persons per year, and that the effects are transitory and fade out within a decade.
2 Using data for the first wave of SHARE, we find that 79% of Austrian couples and 90% of Catalonian couples nonetheless report to have agreed upon a joint property regime.
Table 1
Year of introduction of Unilateral Divorce Laws (UDLs) and exposure to UDLs by country.
(1) (2) (3) (4) (5) (6) (7)
Austria Belgium Denmark France Germany Netherlands Spain
Year of UDL introduction 1978 1975 1970 1976 1977 1971 1981
Couples married before UDL 150 416 160 314 323 255 431
Couples married after UDL 16 92 209 73 48 174 29
Total number of couples 166 508 369 387 371 429 460
Years of exposure to UDLs
Mean 28.5 30.9 31.3 29.0 28.9 33.6 25.5
Std. dev 1.5 2.7 7.6 3.4 3.1 4.1 2.0
Min 18 5 0 2 2 7 5
Max 29 32 37 31 30 36 26
Notes: All the samples contain households aged 50 to 70 who are in their first marriage at the time of the interview and for whom information on all observables is not missing. The year when de facto unilateral, no-fault divorce was first allowed in each country is taken from González and Viitanen (2009) and Kneip and Bauer (2009) .
are reportedinSection 4, which alsoincludes a setof robustnesschecks.We discussthe potential mechanisms through whichexposuretoUDLsmayaffecthouseholdsavingsinSection5.Conclusionsfollow.
2. Dataandinstitutionalcontext
WeusedatafromthesecondandthirdwavesoftheSurveyofHealth,AgingandRetirementinEurope(SHARE)thatwere carriedoutbetween2006–07and2009–10.TheSHAREdatahaveanumberofuniquefeaturesthatmakethemparticularly attractiveforouranalysis.
First,bygatheringharmonisedcurrentandretrospectiveinformationonarepresentativesampleofthepopulationaged 50+inseveralEuropeancountries,SHAREallows ustoconducta cross-countrystudywithouthavingtoworryaboutdata comparability.WepresentevidenceforsevenEuropeancountries– Austria,Belgium,Denmark,France,Germany,the Nether-landsandSpain – whereUDLshavebeenadoptedduringthesecond halfofthetwentiethcentury.Weobtaininformation onthetiming ofintroductionofUDLs fromotherrecentstudies exploitingtheseregime changes,includingGonzález and Viitanen(2009)andKneipetal.(2014).Table1reportstheyearoftheintroductionofde-factoUDLs(thatrangefrom1970 inDenmarkto1981inSpain),thenumberofcouplesmarriedbeforeandafterthechangeindivorcelawsinthe sample, anddescriptivestatisticsforyearsofexposuretoUDLsacrossthesevencountriesincludedinthesample.
Inadditionto theseven countriesthat we consider,two othercountriescovered inSHARE– SwitzerlandandSweden – have alsointroduced UDLs by 2010. However, we are forced toexclude them because the switch to unilateraldivorce occurredeithertooearly (1915in Sweden)ortoolate (2000 inSwitzerland)to obtain informationoncouples that were marriedboth before andaftertheintroduction ofUDLs. Wefind thatour estimatesremain unchangedwhenwe include thesecountriesintheanalysis.We alsohavetodropGreecebecauseofunreliabledataoneconomicvariablesandsample selectionissuesduetotheuseofthetelephonedirectoryasthesamplingframeforSHAREinthatcountry(Mazzonnaand Peracchi,2017).
Second, the third wave of the survey (SHARELIFE) collects retrospective information on manydimensions of the life historiesof respondents,includingrelationship histories.Thisinformation iscrucialfor ourstudybecauseit allows usto focuson couples who are still in their first marriageat the time ofthe survey interview, thereby mitigating the risk of selectingindividualswhohavebeenmarriedmorethanonceandforwhomitwouldbehardtounderstandtheconnection betweendivorce risk and wealthaccumulation.3 The availability ofretrospective life history dataon housing trajectories allowsusalsotoexclude88individualswhoweremarriedinadifferentcountrythantheonewheretheyliveatthetime oftheinterview,whichcouldbeendogenoustochangesindivorcelawsacrosscountries.4
SHARELIFEalso includesinformation on early life conditionsthat we summarise using two indicators.As a proxy for parentalinvestmentinskilldevelopmentearly inlife,we followBrunelloetal.(2017)andconstructanindicator variable takingvalue one ifthe respondenthadmorethan10 booksintheplacewheresheorhewaslivingatage10(i.e.,more thanashelfofbooks,excludingmagazines,newspapersorschoolbooks),andzerootherwise.Asaproxyforfamilywealth andgoodhousingconditionsearlyinlife,weuseanindicatorvariabletakingvalueoneifthenumberofroomsinthehouse wheretherespondentwaslivingatage10wasatleastashighasthenumberofpersonslivinginthehousehold,andzero otherwise.
Third,the second wave of SHARE containsdetailedinformation onhouseholdfinances, which is available onlyat the timeoftheinterview. Onefinancialrespondentperhouseholdisaskedtoanswerseveralquestionsonhouseholdincome andwealth.Wecomputehouseholdnetfinancialwealth,whichconsistsofgrossfinancialassets(bankaccounts,government
3González and Özcan (2013) and Voena (2015) also use married couples in their first marriage. Within our selected countries and age range, 79% of the respondents that were ever married are still in their first marriage at the time of the SHARELIFE interview.
andcorporatebonds,stocks,mutualfunds,individualretirementaccounts,contractualsavingsforhousingandthefacevalue oflifeinsurancepolicies) minusfinancialliabilities.5Wealsocomputehouseholdnettotalwealth,whichisdefinedasthe sumofnetfinancialandrealwealth,wherethelatteristhesumofthevalueoftheprimaryresidencenetofthemortgage, thevalueofotherrealestate,ownedshareofownbusinessandownedcars.6 Wedeflateallthewealthcomponentsusing PPP exchange ratesandCPImeasures into 2006 Euro,so that thevalues are comparableacrosscountriesandover time. InformationonPPP-adjustedexchangeratesandCPImeasuresisobtainedfromtheOECDandnationalsources.7
From thesecond wave ofSHARE,we alsoobtain informationongender, yearofbirth, countryofbirth andofcurrent residence,educationallevels(primary,secondaryorpost-secondaryqualifications)andnumberofchildren.Thesecondwave ofthe survey alsoaskseach respondentaset offourquestionsaimed atmeasuring their abilityto performbasic opera-tions with numbers.On the basis ofthe numberof correctanswers tothe four arithmetic questions,Dewey and Prince (2005)constructanumeracyindexthatrangesfromone tofive.8 The numeracyindexhasnocardinal interpretation,and wecanattach toitanordinalmeaningatbest.Hence, analysingthisoutcomevariablewithalinearregressionwouldnot be a goodapproach. Analternative could be touse an orderedprobit model.However, Bond andLang(2019) show that anyfinding fromordered probitmodels canbe reversed by log-normaltransformations ofthe indexfunction.We there-forerefrainfromusingtheseapproaches, andconstructapositionalindicatortakingvalueone (andzerootherwise) ifthe respondenthas anumeracy scorehigher thanthe median. As shownby Christelis etal.(2010) andLusardi andMitchell (2014),numeracyisarelevantcomponentoffinancialliteracy,andisastrongpredictorofindividualportfoliochoices.From SHARE wave 2,we alsoobtaininformation ontrust onothers,measured ona Likertscale going from0to10, whichwe use to constructa dummy equalto one if the levelof trust of therespondent is above the median. Following Puri and Robinson(2007),wemeasuredispositionaloptimismasthedifferencebetweenself-assessedsurvivalprobabilitiesandthat obtainedfrom actuarial life tablesby gender, country andyearof birth provided by theHuman MortalityDatabase (see
http://www.mortality.org).9 Bothtrust and optimismare correlates of financial developmentand savings. Finally,we use informationonworkinghistoriestogatherinformationonlaboursupplythroughoutthelifecourse.Informationonlabour supply, numeracy, trust andoptimism enablesus toshed light on the potential mechanisms through whichexposure to UDLsmayaffectfinancialwealth.
Inlinewiththe literaturein thisarea(González andViitanen, 2009; González andÖzcan, 2013),we selectcouples in their first marriage and whose head (i.e., the financial respondent) is between50 and 70 years old at the time of the interviewofSHAREwave2.10Wechoosethisageintervaltoobtainasampleofcoupleswhoarearoundretirementandare nottoooldtobestronglyaffectedbysurvivalbias.11
Weusedataatthehouseholdlevelfortheanalysisonsavings anddataatthe individuallevelfortheanalysisonthe potentialmechanisms,i.e.,laboursupply,numeracy, trustandoptimism.Theanalysisattheindividuallevelalsoallows us toshedlight ongenderdifferencesintheimpactofUDLs onthesemediators.Ourfinal samplecontains2690couplesfor thehousehold-levelanalysisonsavingsand4959individualsfortheindividual-levelanalysis.12
Table2reportsdescriptivestatisticsonthemainvariablesusedintheanalysis.Itconsistsoftwopanels,PanelAforthe sampleatthe householdlevelandPanelBforthecorrespondingsampleattheindividuallevel.13 Averagefinancialassets andtotalassetsare respectivelyequalto€ 65,510 and€ 344,105,whilethemedianvaluesofthesevariablesare equalto
5 Unfortunately, no comprehensive measure of pension wealth is available in SHARE for the waves that we consider.
6 Whenever information about a components of wealth is missing, we rely on imputed values reconstructed by SHARE. Imputations have been carried out using state-of-the-art multivariate fully conditional specification methods ( De Luca et al., 2015 ).
7 The information on wealth in SHARE is self-reported and therefore subject to measurement error. However, using individual social security numbers,
Bingley and Martinello (2017) match the Danish subsample of SHARE with administrative data from Danish civil registries and tax reports and show that measurement error for monetary variables in SHARE data is classical, suggesting that SHARE is a reliable source for the analysis of socioeconomic data.
8 The following four questions are asked to SHARE respondents. “1. If the chance of getting a disease is 10%, how many people out of one thousand would
be expected to get the disease? ”; “2. In a sale, a shop is selling all items at half price. Before the sale a sofa costs € 300. How much will it cost in the sale? ”; “3.
A second-hand car dealer is selling a car for € 60 0 0. This is two-thirds of what it costs new. How much did the car cost new? ”; “4. Let us say you have € 20 0 0
in a saving account. The account earns 10% interest each year. How much would you have in the account at the end 2 years? ”. Unlike Christelis et al. (2010) , in generating the numeracy score we treat the few “Don’t Know”s and “Refusal”s that are present in the data as wrong answers instead of dropping or imputing numeracy for individuals who use these answer modes. We thank Rob Alessie for suggesting us this solution.
9 As in Angelini and Cavapozzi (2017) , we elicit respondents’ self-assessed survival probabilities from the question in SHARE: “What are the chances that
you will live to be age T or more? ”. The target age T depends on the age of the respondent at the time of the interview. It is equal to 75 for respondents aged 50–65, 80 for those aged 66–70, 85 for those aged 71–75, 90 for those aged 76–80, 95 for those aged 81–85, 100 for those aged 86–95, 105 for those aged 96–100, and 110 for those aged 101–105. We then use the information from life tables by gender, country and year of birth to compute actuarial probabilities of survival for the same target age.
10 SHARE also interviews the partners of the individuals in the sample irrespective of their age and we do not select couples on the basis of the age of the partner. On average, married women are two years younger than their husbands.
11 This age interval has been considered in several studies that focus on retirement, including Mazzonna and Peracchi (2017) . In a sensitivity analysis, we show that our estimates are qualitatively similar when we consider couples aged 50 to 80 at the time of the interview. We also directly test for UDL-induced mortality in the 50–70 sample, but found no effect of UDL exposure on the likelihood of widowhood at the time of the wave 2 SHARE interview.
12 The size of the individual sample is not equal to twice the size of the household sample because we drop individuals with missing information on the variables used in the analysis. Our results for wealth and for the mechanisms still hold even when we restrict our sample to couples for whom we observe all variables we use as mechanisms for both members. Due to the smaller sample size, however, our estimates for optimism are less precise.
Table 2
Descriptive statistics.
Variable Mean Std. dev.
Panel A: Sample of households. Sample size: 2690
Household net financial wealth ( €) 65,510 123,226
Household net total wealth ( €) 344,105 378,634
Years of exposure to UDLs 29.75 4.716
Age (financial respondent) 59.81 5.818
Female (financial respondent) 0.454 0.498
Year of marriage 1970.9 7.546
Marriage duration (years) 35.86 7.535
High school diploma (financial respondent) 0.343 0.475
College degree (financial respondent) 0.281 0.450
Several books at age 10 (financial respondent) 0.623 0.485
Good housing conditions at age 10 (financial respondent) 0.355 0.479 Panel B: Sample of individuals. Sample size: 4959
High numeracy score 0.557 0.497
High trust 0.565 0.496
Dispositional optimism −0.038 0.259
Years of exposure to UDLs 29.783 4.685
Age 59.772 6.310
Year of marriage 1970.8 7.538
Marriage duration (years) 35.927 7.525
High school diploma 0.342 0.474
College degree 0.265 0.441
Several books at age 10 0.612 0.487
Good housing conditions at age 10 0.347 0.476
Notes: Both samples consider households (Panel A) and individuals (Panel B) aged 50 to 70 who are still in their first marriage at the time of the SHARE interview and for whom information on all variables is not missing. “Several books at home at age 10” is an indicator variable for having 10 or more books at home at age 10. “Good housing conditions at age 10” is an indicator variable for having at least one room per person in the accommodation where living at age 10. “High numeracy score” and “High trust” are indicator variables for numeracy score and trust above the median.
€ 24,545and€ 259,610,confirmingthe skewnessof thesedistributions.Onaverage, coupleshavebeenmarried forclose to36years,havebeenexposed toUDLsfor30years.Individualsare60yearsold onaverageatthetimeoftheinterview, approximately25% haveatleastacollegedegree,andcloseto35%haveatmostahighschool diploma.About60% report that they had more than 10 booksin the place where they were livingat age 10 and35% were livingat age 10 in an accommodationwithatleastoneroomperperson.
3. Empiricalmethodology
3.1. Modelspecification
Toexaminehow exposureto UDLs affectsthesavings ofmarried couples,we estimate thefollowing linearregression model: Yi jk=
α
+β
UDLi jk+γ
YoMi jk+δ
Xi jk+μ
k+η
j+λ
1jk+λ
2 jk 2+ε
i jk (1)wheretheindexijkdenotes acouplei residing incountryj andwhose headisborninyeark.The outcome variableYijk
representsfinancial (ortotal) assets ofcouplei. Assets aremeasured in levelsto includehouseholds withdebt(negative assets).
OurvariableofinterestisUDLijk,definedasthenumberofyearsthecouplewasexposedtoUDLs.Itisasemi-continuous
treatmentvariablethatmeasuresthenumberofyearsofmarriageforcoupleisincetheintroductionofUDLsincountryj. Wepreferthisspecificationtoabinarytreatmentvariableformarriagebefore/afterUDLintroduction,becauseour specifi-cationallows usto considertheintensityofthe exposuretothe UDL-induceddivorce risk:currentsavingsare theresult ofwealthaccumulationoverthelife-cycle.Forinstance,acouplethat wasmarriedwell beforetheintroductionofa UDL mayhavebeenexposed onlymarginallytotheUDL-induced riskofdivorce.Itmaybeincorrect toassumethatthesaving behaviourofthiscoupleshouldbeequivalenttothatofacouplemarriedinthesameyearbutresidinginacountrywhere aUDLwasintroducedearlyon,asthelatterwasexposedtounilateraldivorceriskforalongerperiodoftime.
Insteadofestimatingtheaverage differenceinsavingsbetweencouplesexposed ornot exposedtoUDLs foranygiven periodoftime,ourspecificationallows ustoestimateanaverageeffectperyearofUDLexposure.Giventhatthevariation inUDL exposure inourdata ismostly concentratedbetween 25and35years ofexposure, ourestimated effectshallbe interpreted as the average marginal effect on the stockof savings around retirement age of a one-year change in UDL exposurewithinthisrange.
The modelin Eq.(1)controlsfor yearofmarriage(YoMijk) andbirth cohort fixedeffects (
μ
k) toaccount forpossible trendsinwealthaccumulation.14Wealsoincludeafullsetofcountryfixed-effects(η
j)aswellasasetofquadratic
country-specificcohorttrends(
λ
1jk+
λ
2jk2).Theformercontrolforunobservable,time-invariantdifferencesacrosscountriesthatmayinfluence theaccumulation of households’financial asset, the latterforunobserved cross-countrydifferencesin financial assetsaccumulationovertime.Wealsoincludeasetofindividualpre-maritalcovariatesthatmayaffectfinancialassetsand correlatewithUDLexposure,containedinthevector Xijk anddescribedintheprevioussection.15 Finally,
ε
ijkrepresentsadisturbanceterm.
Oneconcernrelatedtoourspecificationcould bethat,once yearofmarriage,cohortandcountryfixedeffects,aswell ascountry-specificquadraticcohorttrendsandadditionalcontrolsareincluded,thereisnotenoughremaining variationin theyearsofexposuretoUDLstoidentifyitseffectonwealth.However, theR-squaredofaregressionofUDLexposureon allthesecovariatesisequalto0.83(i.e.,wellbelow1),therebysuggestingthatthereissubstantialremainingvariation.
3.2. Identification
Identificationofthecoefficient
β
astheaveragecausaleffectofoneadditionalyearofexposuretoUDLsoncumulated savings is granted by the quasi-natural experimentprovided by the staggered timing of the introductionof UDLs across countries.Ourfirstidentifyingassumptionisthatconditional onyearofmarriage, countryandcohortdummiesaswell as country-specificcohorttrends,thevariationinthenumberofyearsofexposuretoUDLs isasgoodasrandomlyassigned. ThismeansthatthescatteredintroductionofUDLsshallprovideasourceofvariationthatisnot relatedtopredetermined observableorunobservablecharacteristicsofcouplesthatmayexplaintheirsavingbehaviour.Second, since we focus on the sub-sample of couples who are still in their first marriage at the time of the SHARE interview, we alsorequire theabsence ofendogenous dynamicselection outsideofmarriage andintodivorce that takes placedifferentiallywithrespecttoexposuretoUDLs.Forinstance,weneedtoruleoutthepossibilitythatwealthiercouples aremorelikelytosurviveintomarriagewhenexposedtoUDLs,generatingreversecausality.
Focusing onthislatterassumption,we followKneipetal.(2014) andinvestigatewhethertheeffects ofUDLexposure on thehazard ofdivorce isheterogeneouswithrespect toa setofpredeterminedobservable characteristics correlatedto saving propensity.Todo so, we estimate a Cox proportional hazard modelon individual level data.We follow thesame approachasinEq.(1),butinthiscasethetreatmentisanindicatorforbeinginatimeperiodaftertheUDLintroduction. Wealsointeractthisindicatorwithasetofpre-determinedvariablesincludedinvectorXijk,describedabove,aswell asa
broadersetofpre-maritalcovariatesrelatedtofamilybackground(see,e.g.,Gouldetal.,2011),whichmaybelistedamong the determinantsof wealthaccumulation.16 The results reportedin Table3 show that the effectof UDL introductionon the hazard ofdivorce doesnotvary withthesecharacteristics,asthe interactions termsare not statisticallysignificant.17 Byincreasingtherisk ofdivorce, UDLshaveinduceddynamicselection amongmarried couples,butwedonot detectany patternofendogenousselectionwithrespecttothecomprehensivesetofdeterminantsofsavingsthatweanalysed.
Wealsoprovidesupportiveevidenceaboutthejointvalidityofthefirsttwoidentificationassumptionsstatedaboveby showinga setof balancingtests, aimed atverifyingthat married couplesin ourfinal samplewho havebeenexposed to UDLsfordifferenttimeperiodsaresimilarwithrespecttothesecharacteristics.
Table 4reportsthe estimatesof“reverse regressions” of each ofthesepredeterminedcovariates – and oftwo match-specificvariablesmeasuringtheageandeducationgapsbetweenpartners18– onourtreatmentvariable,yearofmarriage, countryandcohortdummies, aswell ascountry-specificquadraticcohorttrends.19 Asweareverifyingbalancingon mul-tiplecovariates, forthisanalysiswe reportboth thestandard p-valuesandtheonesadjusted forthe problemofmultiple hypothesistestingusingthestep-downmethodproposedbyRomanoandWolf(2005)andimplemented,amongothers,by
Heckmanetal.(2013).WefindthattheeffectsofUDLexposureonpredeterminedcovariatesareveryclosetozeroandin mostcasesnotstatisticallysignificant,especiallyoncewetakeintoaccounttheproblemofmultipletesting.20
Inaddition,tofurthersupportthevalidityofourfindings,inthesensitivityanalysis(seeSection4.2)wealsoconsideran imputationstrategyakintoOlivettiandPetrongolo(2008).Inthisexercise,wealsokeepinoursampledivorcedindividuals
14 We include year of marriage in Eq. (1) , as exposure to UDLs is measured in years. If we do not control for year of marriage, then exposure to UDLs will also pick up the effect of marriage duration. Since the timing of marriage could be endogenous to UDL introduction, in Table A.1 in the Appendix we show that there is no response of the timing of marriage to UDL introduction. To further alleviate endogeneity concerns, we also estimate Eq. (1) after excluding year of marriage from the controls and measuring exposure to UDLs as a share of marriage duration, thereby weakening the correlation between UDL exposure and marriage duration. All results are quantitatively comparable to our baseline specification.
15 All specifications also include an indicator variable equal to one if the financial respondent is female and to zero otherwise. 16 Details about these variables are reported in the notes to Table 3 .
17 The main effects are larger in magnitude but not statistically different from the one estimated by Kneip et al. (2014) .
18 These two variables are observed only for couples that are still living together. Therefore, we cannot include them in our duration analysis and in the analysis of selection into marriage.
19 As suggested by Pei et al. (2019) , this test is less subject to concerns regarding attenuation bias than a “balancing” regression of the treatment on all covariates if the latter may be subject to measurement error.
Table 3
The effect of UDL introduction on divorce – Cox proportional hazard model.
(1) (2) (3)
Hazard rate Hazard rate Hazard rate
After UDL introduction 1.826 ∗∗∗ 1.803 ∗∗∗ 1.991 ∗∗∗
(0.169) (0.174) (0.424)
After UDL introduction × …
Experienced financial hardship before age 18 0.518 ∗
High school diploma 1.059
College degree 0.995
Several books at age 10 0.977
Good at math 1.193
Good housing conditions at age 10 0.946
Poor housing sanitation at age 10 0.920
Parents drank, smoked or had mental health issues 0.838
Missed school for 1 + months in childhood 0.711
Had no serious childhood diseases 1.516
Parents had professional occupations 1.165
Did not live with mother at age 10 0.796
Did not live with father at age 10 1.148
Joint significance of all interactions terms ( p -value) 0.354
Observations 8160 8160 8160
Covariates No Yes Yes
Notes: The table reports the coefficients of ”After UDL introduction” and its interaction with pre-determined covariates on the hazard rate of divorce. All models control for year of marriage, country and cohort fixed effects, and country-specific quadratic cohort trends. Additional covariates included in Columns (2) and (3) are the ones for whom the interaction with ”After UDL introduction” are reported in Column (3). Good at math is an indicator variable equal to 1 if the respondent was better than average classmate in math at primary school, and to 0 otherwise. Good housing condition is an indicator variable equal to 1 if there were at least as many rooms as people in the accommodation where the respondent was living at age 10, and to 0 otherwise. Poor housing sanitation is an indicator variable equal to 1 if there was no cold running water or inside toilet in the accommodation where the respondent was living at age 10, and to 0 otherwise. Serious childhood diseases listed in the survey are: Infectious disease (e.g. measles, rubella, chickenpox, mumps, tuberculosis, diphtheria, scarlet fever); Polio; Asthma; Respiratory problems other than asthma; Allergies (other than asthma); Severe diarrhoea; Meningitis/encephalitis; Chronic ear problems. Standard errors clustered by country and year of marriage reported only for the main effects. ∗∗∗p < 0.01, ∗∗p < 0.05, ∗p < 0.1.
andcouples whereatleastone memberhasdivorcedinthepast,whichare droppedfromourmainanalysis.21Forthese groups,weusetheobservedlevelofwealthasan imputedvalueforthelevelofwealththattheywouldhaveexperienced hadthey(ortheircurrentpartners)notdivorced.WethenestimatetheeffectsofUDLsonwealthusingmedianregressions inthislargersample. As highlightedby Olivetti andPetrongolo (2008),medianregressionshavea veryappealing feature forimputationmethods.In fact,the estimatessolelydepend onthe relativestandingofobservations withrespectto the medianone,andnot onthe specificimputedwealth value.Thus, aslongashouseholdskeep onbeingon thesame side ofthemedianofthewealthdistributionbothincaseofmarriagecontinuationandincaseofseparation,imputationsand medianregressionallowustoovercomedynamicselection.22
Anotherconcernforouridentificationstrategy wouldbe thepresence ofan effectofUDLs onselection intomarriage ifdifferenttypesofindividualsdecide togetmarriedasaresultoftheintroductionofUDLs,thereby generatingselection bias.Toverifywhetherthisisthecase,weuseSHAREdataonallindividualswhoevergotmarriedinourchosencountries andagerange,andemployadifference-in-differencesmodel,inwhichweregressthepre-determined characteristicsused inthepreviousanalysisonanindicatorvariableequalto1iftheindividualmarriedforthefirsttimeaftertheintroduction ofUDLs,andto0otherwise,countryfixed effects,yearoffirstmarriagefixedeffects,country-specificquadratic trendsin theyearoffirst marriageandgender.23 The resultsare reportedinTable 5:since wedo notfind anystrongevidenceof changesincharacteristicsofspousesattheirfirstmarriageasUDLsareapproved,weconcludethatitisunlikelythatUDLs affectedselection intomarriage. Wealso approachthisissuemore directlyinTable A.1inthe Appendix.Inthisanalysis, we consider the sampleof all individuals aged 50–70 and residing in one of the seven countries covered inthis study, andweestimate theeffectsofexposure toUDLssincetheageof16(the minimummarriageageinoursample)onbeing evermarried (columns 1and 2) andon age atfirst marriage conditional on marriage(columns 3 and4). In columns 2 and4,wealsointeractUDLexposurewiththeindividualcovariates,inordertoassesspotentialheterogeneouseffects.The regressionsareconditional oncohortandcountryfixed effects,country-specificquadratictrendsandindividualcovariates (excludingyearofmarriage).The empiricalresultsshow that UDLexposure since16has noimpacton theprobability of
21 We consider each of these individuals as a couple – as each individual is the survivor of a marriage that either ( a ) is still in place but is not the first for the other member of the couple, or ( b ) ended up in a divorce.
22Bertoni et al. (2015) is another application of median regression and imputation to correct for dynamic selection.
23 Even in this case, we report both the standard p -values and the ones adjusted for the problem of multiple hypothesis testing using the step-down method proposed by Romano and Wolf (2005) .
Table 4 Balancing tests.
(1)
Exposure to UDLs
Coefficient Standard p -value Corrected p -value Experienced financial hardship before age 18 −0.001 0.343 0.888
High school diploma 0.003 0.400 0.984
College degree 0.012 0.006 0.083
Partners have the same educational level −0.009 0.087 0.581
Absolute age gap between partners −0.009 0.788 0.992
Several books at age 10 0.004 0.348 0.984
Good at math 0.010 0.055 0.470
Good housing conditions at age 10 −0.001 0.810 0.992
Poor housing sanitation at age 10 −0.004 0.310 0.976
Parents drank, smoked or had mental health issues 0.004 0.411 0.984 Missed school for 1 + months in childhood −0.000 0.964 0.992
Had no serious childhood diseases −0.001 0.809 0.992
Parents had professional occupations −0.003 0.248 0.920
Did not live with mother at age 10 −0.001 0.376 0.984
Did not live with father at age 10 −0.006 0.027 0.290
Observations 2690
Notes: The table reports the coefficient of exposure to UDLs derived by reverse regressions of the pre-determined covariates listed in in each row on exposure to UDLs. All models control for year of marriage, country and cohort fixed effects, and country-specific quadratic cohort trends. Household-level sample. Standard p -values as well as p -values corrected for multiple hypothesis testing using the stepdown procedure of Romano and Wolf (2005) are reported. We use bootstrap clustered by country and year of marriage, based on 250 iterations of the stepdown procedure.
Table 5
Selection into marriage.
(1)
Married after UDL introduction
Coefficient Standard p -value Corrected p -value Experienced financial hardship before age 18 0.001 0.847 0.988
High school diploma 0.002 0.910 0.988
College degree −0.006 0.784 0.988
Several books at age 10 0.005 0.800 0.988
Good at math −0.002 0.946 0.988
Good housing conditions at age 10 0.001 0.955 0.988
Poor housing sanitation at age 10 −0.017 0.433 0.988
Parents drank, smoked or had mental health issues −0.003 0.988
Missed school for 1 + months in childhood 0.004 0.672 0.988
Had no serious childhood diseases 0.018 0.140 0.912
Parents had professional occupations 0.030 0.049 0.474
Did not live with mother at age 10 −0.014 0.062 0.772
Did not live with father at age 10 0.004 0.730 0.988
Observations 7723
Notes: The table reports the difference-in-differences effects of marriage after UDL introduction on the pre-determined covari- ates listed in in each row on a indicator variable for being married after UDL introduction. All models control for year of marriage fixed effects, gender and cohort fixed effects, and country-specific quadratic trends in year of marriage. The sample includes all SHARE respondents in our countries and age range that have ever been married. Year of marriage refers to the first marriage. Standard p -values as well as p -values corrected for multiple hypothesis testing using the stepdown procedure of
Romano and Wolf (2005) are reported. We use bootstrap clustered by country and year of marriage, based on 250 iterations of the stepdown procedure.
beingevermarriedoronageatfirstmarriage.Inaddition,thesezeroaverageeffectsdonotmaskanyheterogeneityalong the observabledimensionsthat we consider, sincethe interactions withtheindividual covariates aregenerallysmall and jointlyinsignificant,asconfirmedbythep-valueoftheFtestsreportedatthebottomofcolumns2and4.
At this stage, it is worth remarking that we cannot exclude that forces other than those observed are important to determine selection effects.However, although we wish toprovide evidence onthe absence ofselection withrespect to preferencesandothersocialnormsthatledtotheintroductionofUDLsacrosscountries,weareconstrainedbydata avail-ability,andhavetofocusonlyonvariablesforwhichatleastsome roughproxythat pre-datesthetreatmentisobserved. Still,webelievethatthebreadthofoursurveydatahelpsustoalleviatethisconcern.
A further assumption required to attribute a causal interpretation to our estimated effects is that there is no other country-specific unobserved shock that affects saving behaviour and whose timing coincides with that of the adoption of UDLs – generating omittedvariables bias.In Section 4.2,we provide support forthisassumption inthree ways.First,
Table 6
Effects of UDLs on financial wealth. Median and mean regressions.
Dep. var.: financial wealth ( €) Median Mean
(1) (2) (3) (4)
Exposure to UDLs 1857 ∗∗∗ 1493 ∗∗∗ 3309 ∗∗∗ 2581 ∗∗
(537) (536) (1,096) (1,024)
Observations 2690 2690 2690 2690
Covariates No Yes No Yes
Median dep. var. 24,545 24,545 – –
Mean dep. var. – – 65,510 65,510
Notes: The table reports the effects of exposure to UDLs on mean and median financial wealth. Mean effects estimated via OLS regressions, median effects via Recentered Influence Function (RIF) unconditional quantile regressions. All models control for year of marriage, country and cohort fixed effects, and country-specific quadratic cohort trends. The covariates included in Columns (2) and (4) are indicator variables for having a high school diploma, a college degree, several books at age 10, and good housing conditions at age 10. Household-level sample. Standard errors clustered by country and year of marriage are reported in parentheses. ∗∗∗p < 0.01, ∗∗p < 0.05, ∗p < 0.1.
weshow thatourresultsstill holdwhenwe excludefromoursampleone countryatatime, allowingustoruleout the possibilitythat potentialconcurringshockshappeninginsinglecountriesarethemaindriversofourfindings.Second,we estimateaplaceboregressioninwhichweswitchtheyearofintroductionofUDLs acrosscountries.Third,weruna sensi-tivityanalysisinwhichwereplacethecountry-specificquadratictrendswithquadratictrendsinGDPpercapita.
Finally,whilethecountryandtimevariationofUDLsofferanappealingidentificationstrategyfortheestimationofthe effectofdivorcelawsonwealthaccumulationlaterinlife,couplescanadjusttheyearofmarriageinresponsetoexpected changesinUnilateralDivorceLawreforms.Asaresult,theanticipationoftheintroductionofUDLsbyspouseswouldviolate theidentifyingassumptions describedabove.Toverifythatendogenousadjustmentsofthetimingofmarriageinresponse tothe anticipation ofUDL introduction isnot responsible for ourfindings, we show that our resultsstill hold whenwe excludecouplesmarried ina1-year interval aroundthe yearofadoption ofUDLs,when (potentiallyendogenous)sorting intomarriagebefore/afterthelawchangesismorelikelytohavetakenplace.
3.3.Estimationandinference
WeestimateEq.(1)byOLSwhenfocusingonmeaneffects,andusingRecenteredInfluenceFunction(RIF)unconditional quantileregressions(Firpoetal.,2009)torecovertreatmenteffectsonthemedianorotherquantilesofthewealth distribu-tion.Throughouttheanalysis,weclusterstandarderrorsbycountryandyearofmarriage,thelevelofvariationofexposure toUDLs.
4. Empiricalresults
4.1. Mainresults
Table6reportsestimatesof thelong-termeffectsofexposure toUDLs on themedian(see columns1and2) andthe mean(see columns 3and 4) offinancial assetsof married couples.The results incolumns 1and 3control for theyear ofmarriage, cohortandcountryfixed-effects, aswell asquadraticcountry-specific cohorttrends, whilecolumns2 and4 alsocontrol forpre-marital covariates invectorXijk.The estimatesincolumns1 and2suggestthat an additionalyearof exposuretoUDLsleadstoanincreaseinmedianfinancialwealthof€ 1857to€ 1493,dependingonthespecification,which correspondtoanincrease ofapproximately7.5%to6% relativetomedianfinancialwealth,respectively. TheOLSestimates reportedincolumns3and4portrayasimilarpicture:wefindthatanadditionalyearofexposuretoUDLsincreasesmean householdsavingsby€ 3309to€ 2581,dependingonthespecification.Theseeffectscorrespondtoapproximately5%to4% ofmeanfinancialwealth,respectively.
4.2.Robustness
Inthissectionwedescribehowourestimateschangewhenweusedifferentsamplesorspecifications.
First,wenoticethattheslightchangesincoefficientsduetotheinclusionofcovariatesinTable6maysignalaproblem ofomittedvariablesbias.Toverifywhetherthisisindeedthecase,weapplytheproceduresuggestedbyOster(2019),and estimatehowimportantselectiononomittedvariablesshouldbewithrespecttoselectionontheincludedones(theratio betweenthetwobeingcalled
δ
) toexplainawaytheestimatedtreatmenteffect.Forexample,δ
=2wouldimplythatthe omittedvariableswouldneedtobetwiceasimportantastheincludedonestoproduceatreatmenteffectofzero.According toOster (2019)andto theprevious workon thetopicbyAltonji etal.(2005),avalue ofδ
above 1issufficientto claimTable 7
Effects of UDLs on financial wealth. Median regressions. Robustness tests.
Median
Dep. var.: financial wealth ( €) (1)
Panel A. Including as controls all the variables used in the balancing tests.
Exposure to UDLs 1705 ∗∗∗
(596) Panel B. Cluster by country (Wild boostrap p -values reported in brackets).
Exposure to UDLs 1493
[0.10] Panel C. Including Sweden and Switzerland.
Exposure to UDLs 1293 ∗∗
(557) Panel D. Drop Catalonia and Austria, where by default asset property regime is separated.
Exposure to UDLs 1442 ∗∗∗
(576) Panel E. Drop couples married +1/ −1 years around UDL introduction.
Exposure to UDLs 1337 ∗∗
(581) Panel F. Age range: 50 to 80.
Exposure to UDLs 1050 ∗∗∗
(446) Panel G. Placebo test: switched order of UDL year of introduction by country.
Exposure to UDLs 822
(601) Panel H. Including quadratic trends in GDP per capita at birth by country and cohort
instead of country-specific quadratic cohort trends
Exposure to UDLs 1704 ∗∗∗
(517)
Covariates Yes
Notes: Unless otherwise stated, the table reports the effects of exposure to UDLs on median financial wealth, estimated via Recentered Influence Function (RIF) unconditional quantile regressions. All models control for year of marriage, country and cohort fixed effects, country-specific quadratic cohort trends, and indicator variables for having a high school diploma, a college degree, several books at age 10, and good housing conditions at age 10. Household-level sample. The additional covariates included in Panel A are listed in Table 4 . Sample sizes: Panel A: 2181; Panels B, G, H: 2690; Panel C: 3149; Panel D: 2490; Panel E: 2343; Panel F: 3357. Standard errors clustered by country and year of marriage are reported in parentheses. In Panel B, wild-bootstrap p -values are obtained as in Cameron et al. (2008) (the number of countries is equal to 7). In Panel G, the placebo years of UDL introduction by country are the following: Austria: 1971; Belgium: 1977; Denmark: 1981; France: 1976; Germany: 1975; Netherlands: 1978; Spain: 1970. ∗∗∗p < 0.01, ∗∗p < 0.05, ∗p < 0.1.
robustnessoftheempiricalresultstoomittedvariablesbias.24Weestimateavalueof
δ
equalto2.71formedianregression and2.67 formeanregression.Theseresultsindicatethat,inbothcases,selectiononomittedvariablesshouldbeabout2.7 timesstrongerthanselectionontheincludedonestodriveourestimatedtreatmenteffecttozero,thusalleviatingconcerns relatedtocoefficientinstabilityandomittedvariablesbias.Inwhatfollows,wepresentother robustnesstests. Forsimplicity,we mostlyfocusonthespecificationincolumn2of
Table6butresultsholdalsofortheotherspecifications.
In Table A.2 inthe Appendix we report results of ourimputation strategy to address the issue of dynamicselection describedin Section 3.2andbased onmedian regressionsestimated ina samplethat includes alsodivorced individuals. Forthem, weuse observedwealthasa measure ofthepotential wealththat they wouldhaveexperienced hadthey not divorced.FollowingOlivettiandPetrongolo(2008),theassumptionforconsistentestimationoftheeffectsofUDLexposure inthisfullsampleisthatthepositionofthesecouples withrespecttothemedianofthewealthdistributionwouldhave beenthesame,hadthey notdivorced. Theresultstillshowsa positiveandsignificanteffectofUDL exposureonsavings, confirmingthatdynamicself-selectionintomarriageduetoUDLexposureisnotamajorsourceofconcernforouranalysis. AdditionalrobustnesstestsarereportedinTable7.First,inPanelAweshowthatourmaineffectisqualitativelysimilar when we control forall the covariates includedin the balancingtests, which are strongly relatedwiththe need (orthe possibility) to save and vary by cohort, andthus exposure to UDL. This resultfurther mitigates concerns relatedto the omitted variables bias discussed above.25 Second, Panel B showsthat thesignificance of our main effectis not strongly
24 The procedure requires to choose a value of Rmax, the maximum attainable level of R -squared. As argued by Oster (2019) , a value of R -squared = 1 is too conservative, while a reasonable choice is to set Rmax = 1.3 times the R -squared of the model with all controls. In our case, this is equal to 0.23 for the median regression and to 0.16 for the mean regression.
25 In fact, our main result is also robust and still pass the tests proposed by Oster (2019) , when we include among the covariates a set of post-treatment “bad” controls, that includes the number of children, a dummy for currently living in a rural area, indicators for being currently employed, retired, or other for both members of the couple, and labour market experience of both members of the couple. The estimates are available from the authors.
affected when we cluster standard errors by country instead of country and year of marriage. As there are only seven countriesinourdata,weobtainp-valuesthatarerobusttoclusteringatthecountrylevelusingwildbootstrap.
Third,inPanelCweshowthatthemainresultisnotaffectedbytheinclusionofSwedenandSwitzerland,whereUDLs havebeenadoptedeithertooearly(1915inSweden)ortoolate(2000inSwitzerland)toobserveenoughcouplesmarried bothbeforeandaftertheintroductionofUDLs.InPanelD,weshowthatourmainresultstillholdswhenwedropfromthe sampleAustriaandCatalonia,whereassetpropertyisseparatedbydefault.
Ouridentificationstrategyrequirestheabsenceofsortingintomarriageonthebasisofsavingpropensitybeforeorafter theintroductionofUDLs.Toverifythatourmainresultisnotonlydrivenbypotentialviolationsofthisno-sortingcondition, weshowinPanelEthatoureffectisqualitativelysimilarwhenweestimateEq.(1)andexcludefromthesamplespouses whowere marriedintheclosevicinityofthedivorcelaws(i.e.,oneyearbefore/afterthechangeinthelaws). Tovalidate ourfindingsonawideragerange,wealsoincludehouseholdswhoseheadisbetween71and80andshowinPanelFthat ourmainresultstillholds.
Aremaining issueabout ouridentificationstrategy concerns the possibilitythat, ifour modelwasmis-specified, UDL exposure could be picking up some concurring country-specifictrend. We deal withthisconcern intwo ways. First,we run a placeboexercise, wherewe switch the orderof theyears of introductionof UDLs across countriesby maximising thedistance withrespect to theoriginal distribution.26 If ourmodel iscorrectly specified,we should find nosignificant effectofUDLs onwealthunderthisplaceboassignment.TheresultreportedinPanelG supportsthisview.27 Second,asa specificationtest,we alsosubstitutethecountry-specificquadratictime trendswithquadratictrendsinGDPper capitaat birthbycohortandcountry(thedataaretakenfromtheMaddisontables).TheeffectpresentedinPanelHissimilartothe oneobtainedwithourmainspecification. Giventheconcernraised byWolfers(2006) thatcountry-specificcohort trends mightinadvertentlypickupsomedynamicsinducedbythepolicychangeandleadtobiasedresults,wepresentadditional sensitivitiestothespecificationoftrendsinTableA.3intheAppendix.Resultsforourmainspecificationarealwaysstable irrespective ofwhether we omittrends, include linearor quadraticcountry-specific cohort trends,or linearor quadratic trendsinGDPpercapitaatbirthbycohortandcountry.Inaddition,goodness-of-fittests(i.e.,AICandadjustedR-squared) suggestthatthespecificationwithquadraticcountry-specificcohorttrends– thatwechoseasourbaseline – hasthebest fit.
Anadditionalconcernregardsthe sensitivityofourfindingswithrespectto thecountriesincludedinthesampleand towhetherthesearedrivenby aspecificcountry. Todispelthisconcern,TableA.4intheAppendixreportstheestimated effectsonmedianwealthwhenwedroponecountryatatimefromoursample:theestimatedcoefficientsontheexposure toUDLsremainfairlystable,rangingfrom€ 925to€ 2131.
Afinal concern withour empirical specificationforthe household-level regressions could be related toour choice of indexingallcovariates – includingbirthcohort– to thehouseholdhead.Ifold husbandsrespondinwealthycouplesand youngerwivesin lesswealthy couplesthis mightbias theestimates.We have carriedout two testsin thisregard. First, werepeat ourindividual-level analysisonthebalanced sampleofcouples forwhomboth membersare interviewed,this time considering asdependent variablea binaryvariabletaking value 1ifthe individual is thefinancial respondentand 0otherwise.We carry outthis analysisseparatelyforwomen andmen. Thiscan be interpretedasa testforselection of financialrespondentsbygenderasafunctionofexposuretoUDLs,allowingforgender-specifictrendsandfixedeffects.The results(notreportedtosavespacebutavailablefromtheauthors)suggestthatthereisnorelationshipbetweendifferential exposureto UDLs andtheprobability that a womanor amanis selectedasthe financialrespondent. Second, we repeat ourmainanalysisforsavings atthehouseholdlevelincludingfixed effectsandtrendsforthecohortofbothmembersof thecouple.Clearly,thiscanonlybedoneforthebalancedsampleforwhominformationisavailableforbothpartners.The estimatedUDL effect remains qualitatively unaltered withrespect to ourbaseline, although it becomes slightlylarger in magnitude.
4.3.Quantiletreatmenteffectsandheterogeneitybyeducation
Toinvestigatetheheterogeneouseffectsacrossthedistributionofhouseholdsavings,wereportinTable8theestimates ofunconditional quantile treatment effects obtainedby RIF regressions (Firpo etal., 2009) andthe specificationused in column2 of Table 6. The effect of exposure to UDLs goesup from€ 607 to € 4257 as we move fromthe 25th to the 75thpercentile,andthetreatmenteffectsareevenmorepronouncedwhenwecomparethe10thwiththe90thpercentile. Inother words, thelong-termeffects ofexposure to UDLs arelarger forricherhouseholds. Toreconcileour resultswith those obtainedinthe literature, we note that using USdata, Voena (2015) also findsan increase inhousehold assetsin responsetotheintroductionofUDLsincommunitypropertystates.Inparticular,theauthoruncoversthatthecoefficients estimated using medianregression are substantially smaller than those obtained from the OLS, thereby suggesting that
26 The first three countries to introduce the UDLs are assigned the years of the three most recent countries and all other countries are switched back by three positions: Denmark is assigned year 1977, the Netherlands 1978, Belgium 1981, France 1970, Germany 1971, Austria 1975 and Spain 1976.
27 To gain further credibility into this placebo, following Chetty et al. (2009) , we have also estimated our model after carrying out 500 random permuta- tions of years of exposure across the seven countries considered in the analysis. This provides an estimate of the empirical distribution of the effect under the null hypothesis of no effect. Our baseline estimate is well above the 95th percentile of this distribution.
Table 8
Unconditional quantile treatment effects of UDLs on financial wealth. Dep. var.: financial wealth ( €) (1) Quantile 10 Exposure to UDLs −134 (206) Quantile 25 Exposure to UDLs 607 ∗∗ (294) Quantile 50 Exposure to UDLs 1493 ∗∗∗ (536) Quantile 75 Exposure to UDLs 4528 ∗∗∗ (1438) Quantile 90 Exposure to UDLs 6143 ∗∗ (2921) Observations 2690 Covariates Yes
Notes: The table reports the unconditional quantile treatment effects of exposure to UDLs on financial wealth. Unconditional quantile treatment effects are estimated via Recentered Influence Function (RIF) regres- sions. All models control for year of marriage, country and cohort fixed effects, country-specific quadratic cohort trends, and indicator variables for having a high school diploma, a college degree, several books at age 10, and good housing conditions at age 10. Household-level sample. Standard errors clustered by country and year of marriage are reported in parentheses. ∗∗∗p < 0.01, ∗∗p < 0.05, ∗p < 0.1.
Table 9
Heterogeneous effects of UDLs on financial wealth by education. Median regressions. Dep. var.: financial wealth ( €) Median
(1) (2)
High education Low education
Exposure to UDLs 5817 ∗∗∗ 1125 ∗∗
(1756) (487)
Observations 757 1933
Covariates Yes Yes
Median dep. var. 55,312 16,576
Notes: The table reports the heterogeneous effect of exposure to UDLs on median finan- cial wealth by education, estimated via Recentered Influence Function (RIF) uncondi- tional quantile regression. The model controls for year of marriage, country and cohort fixed effects, country-specific quadratic cohort trends, and indicator variables for hav- ing a high school diploma, a college degree, several books at age 10, and good housing conditions at age 10. High education is for household heads with tertiary degree, low education for secondary or below. Household-level sample. Standard errors clustered by country and year of marriage are reported in parentheses. ∗∗∗p < 0.01, ∗∗p < 0.05, ∗p < 0.1.
richerhouseholdsexhibitagreaterresponsetotheUDLs.28 Importantly,thisresultconfirmsourfindingsthattheeffectof UDLsisparticularlypronouncedamongmoreaffluenthouseholds.29
In a similar fashion,in Table 9we report the heterogeneous effectson median wealthby the levelof education.We distinguishbetweenhouseholdswhoseheadhasatertiarydegreeandthosewithasecondarydegreeorlower.Resultsshow thattheeffectofUDLexposureonwealthismuchlargeramongthehighlyeducatedthanamongtheloweducated(€ 5817 vs.€ 1125).Thisresultishelpfulfortworeasons.First,educationisamajordeterminantoflate-lifewealth,andtherefore,
28 Yet, differently from our study, Voena (2015) does not dig deeper into the heterogeneous impacts of UDLs across the distribution of household savings. We believe that our paper fills this gap, by analysing the effects to the UDL introduction at different points of the wealth distribution. We are not aware of other studies that conducted a similar analysis.
29 To put the magnitude of our results into perspective, we used the publicly available data by Voena (2015) , and calculated that in her analysis the increase in total assets is equal to about € 3500 per year of exposure to UDLs, compared to about € 50 0 0 in our study. We believe that the larger magnitude of our estimated effect can be explained by two reasons. First, we consider a sample of older people, who are on average richer. Second, the individuals in our sample are exposed to UDLs for a much longer period of time (29.7 years in our case vs. about 17.58 years in Voena ’s, 2015 analysis). Given that the effects obtained by Voena (2015) increase with the years of introduction of unilateral divorce (see Panel A of Fig. 1, p. 2315), we would expect that these effects should become larger the longer people are exposed to UDLs.
Table 10
Effects of UDLs on total wealth. Median regressions.
Dep. var.: total wealth ( €) Median (1)
Exposure to UDLs 4988 ∗∗
(2423)
Observations 2690
Covariates Yes
Median dep. var. 259,610
Notes: The table reports the effect of exposure to UDLs on median total wealth (the sum of real and financial wealth), estimated via Recentered Influence Function (RIF) unconditional quantile regression. The model controls for year of marriage, country and cohort fixed effects, country- specific quadratic cohort trends, and indicator variables for having a high school diploma, a college degree, several books at age 10, and good housing conditions at age 10. Household-level sample. Standard errors clustered by country and year of marriage are reported in parentheses. ∗∗∗p < 0.01, ∗∗p < 0.05, ∗p < 0.1.
detecting heterogeneous effects by education may help to explain the differential effects uncovered atvarious points of the wealth distribution. Second, it is reasonableto assume that better educated people were more informed about the introductionofUDLsaswellasmoreknowledgeableabouttheirconsequences,andtherefore,exhibitedagreaterresponse tothechangeinthedivorceregime.
4.4.Effectsontotalwealth
Asa furtherextension, wealso verifywhetherourmainfindings still holdwhenwe considera differentdefinitionof householdsavings.Tothisaim,weconductaparallelanalysisusingtotalwealth,i.e.,thesumofrealandfinancialwealth, asthedependentvariable.Theeffectformedianwealthfromaspecificationidenticaltotheoneincolumn2ofTable6is displayedin Table 10, andis in line withthe one reportedfor financial wealth (see Table 6), whereby longer exposure toUDLs increaseshouseholdsavings. Theestimatedeffectisslightlysmallerinrelativetermswithrespectto theonefor financial wealthonly, as it ranges around 2–2.5%of the mediantotal wealth inthe sample. As reported in TableA.5 in theAppendix, even inthis casewe estimate larger effects at thetop of the totalwealth distribution. Thissuggeststhat ourresults are mostlydriven by financial wealth,andare consistent withthe idea that real assetsrepresentthe wealth componentthatismostdifficulttochange.
5. Potentialmechanisms
Whatcouldbe themechanismsunderlyingourresults? Inwhatfollows,we showthatwomen inparticularresponded tothe risk ofunilateral divorceby increasing their laboursupply, improvingtheir numeracy, displayinga higherlevel of trustinothersanddispositionaloptimism.Byworking, women earnasalary, whichallowsthem toincrease their saving potential.In addition,vanRooij etal.(2012) documenta positiveassociation betweenfinancialliteracy andwealth accu-mulation,whileLusardi andMitchell(2014),Christelis etal.(2010) andBanksetal.(2010) showthat people withbetter numericalabilitiesarebetterpreparedforretirementintermsofsavings,makemoresophisticatedinvestmentchoicesand de-cumulateassetsatafasterpaceafterretirement– inaccordancewiththepredictionofastandardlife-cyclemodel.Guiso etal.(2008)highlighthow socialcapitalandtrust help financialdevelopment, andJiangandLim(2016) show that trust hasacausal positiveeffectonhouseholdnetworth, whichismorepronounced forwomen thanformen. Relatedtothis literature,PuriandRobinson(2007)showthatdispositionaloptimism,definedashavingpositiveexpectationsaboutfuture events,is alsorelatedto savings:optimistssavemore.Althoughinoursetup weare notableto providecausalestimates aboutthe linkbetween each ofthesepotential mechanisms andsavings, finding that exposure to UDLs increaseslabour supply,numeracy,trustanddispositionaloptimismisstillindicativeabouttherelevanceofthesepotentialmechanisms.30
Weproceedintwosteps.First,theavailabilityofretrospectiveindividual-levellifehistoriesdataonlaboursupplybyyear allowsustoestimate difference-in-differencesmodelsfortheeffects ofUDLintroductiononlaboursupply.Thesemodels allowustoenhanceinternalvalidityandprovidetestsforparalleltrendsbeforetheintroductionofthelaws,tomakesure thattheeffectwepickupisnotduetorisingtrendsinfemalelaboursupplybutisagenuinetreatmenteffect.
Inthisanalysis,weconsidertheyearsbetween1965and1980.Westartin1965,5yearsbeforethefirstintroductionof UDLsinthecountriesofinterest(inDenmarkin1970)tohaveameaningfulpre-treatmentperiodinallcountries,andstop in1980becausefrom1981 onwardsall countriesareina UDLregime, andwe donot haveacontrol group anymore.To avoidissuesrelatedwithselectionintomarriage,weonlyconsiderindividualsinoursamplethatgotmarriedbefore1970, 30 We have also tested for potential fertility effects of UDLs as a mechanism, but we found no evidence that couples reacted to the UDL introduction by modifying their number of children.
