II.A. Prize-Linked Savings Accounts

Prize-linked savings (PLS) accounts incorporate a lottery element instead of paying interest (Kearney et al. 2011). PLS accounts have existed in Sweden since 1949 and were originally subsidized by the government. The subsidies ceased in 1985, at which point the government authorized banks to offer PLS products under new names. Two systems were put into place. The savings banks (Sparbankerna) started offering their clients a PLS product known as the Million Account (Miljonkontot), whereas the remaining banks joined forces and offered a PLS product known as the Winner Account (Vinnarkontot). Each system had over 2 million accounts, implying that one in two Swedes held a PLS account.

Our analyses are based on two sources of information about the Winner Account system that were retrieved from the National Archives: a set of microfiche images with account data and prize lists printed on paper (see PLS Figures II–IV in the Online Appendix). One separate microfiche volume exists for each monthly PLS draw that took place between December 1986 and December 1994 (the “fiche period”). Each volume contains one row of data for each account in existence at the time, with information about the account number, the account owner’s PIN, and the account balance. The prize lists, which are available for each draw until 2003, contain information about the account numbers of winning accounts and the prizes won (type of prize and prize amount). The prize lists do not contain the account owner’s PIN, so the fiches are needed to identify the unique mapping from account number to PIN. After the fiche period, we can identify the PIN of winners as long as the winning account was active during the fiche period.

Two research assistants working independently manually entered each prize list. We relied on optical character recognition (OCR) technology to digitize the microfiche cards, which contain almost 200 million rows of data. We also supplemented the OCR-digitized data with manually gathered data for all accounts that won 100,000 SEK or more during the fiche period. In the Online Appendix, we provide a detailed account of how we processed the digitized data to construct a monthly panel for the years 1986 to 1994 with information about accounts, their balance, and the PIN of the account holder. Our quality checks, which rely in part on the manually collected data, showed that our algorithm was very effective at correctly mapping prize-winning accounts to a PIN and determining their account balances (Online Appendix III.C–III.E).

PLS players could win two types of prizes: fixed prizes and odds prizes. To select the winners, each account was first assigned one unique integer-valued lottery ticket per 100 SEK in balance. Each prize was then awarded by randomly drawing a winning ticket. Fixed prizes varied between 1,000 and 2 million SEK net of taxes and (conditional on winning) did not depend on the account balance. The odds prizes instead paid a multiple of 1, 10, or 100 of the account balance to the winner, with the prize amount capped at 1 million SEK. Conditional on winning an odds prize, an account with a larger balance thus won a larger prize (except when the cap was binding).

To construct the cells used in our adult analyses, we use different approaches depending on the type of prize won. For fixed-prize winners, our identification strategy exploits the fact that in the population of players who won exactly n fixed prizes in a particular draw, the total sum of fixed prizes won is independent of the account balance (see Online Appendix III.I for a formal treatment). For each draw, we therefore assign winners to the same cell if they won an identical number of fixed prizes in that draw and define the treatment variable as the sum of fixed prizes won. Several previous papers have used this identification strategy (Imbens, Rubin, and Sacerdote 2001; Hankins and Hoekstra 2011; Hankins, Hoekstra, and Skiba 2011). Because it does not require information about the number of tickets owned, we can use it for fixed prizes won during and after the fiche period.

For odds-prize winners, matching on number of prizes won and draw is insufficient because winners of larger odds prizes, on average, have larger account balances (which may be correlated with unobservable determinants of health). We therefore match individuals who won exactly one odds prize to controls who won exactly one prize (odds or fixed) in the same draw and whose account had a near-identical balance to that of the winning account.⁴ A fixed-prize winner who is successfully matched to an odds-prize winner is moved from the original fixed-prize cell to the cell of the odds-prize winner. After the fiche period, we do not observe account balances; therefore we restrict attention to odds prizes won during the fiche period (1986–1994).

The final sample is restricted to prize-winning accounts only because we find some indications that in the full panel, nonwinning accounts in a given draw are not missing at random.⁵ For the prize-winning accounts, we were able to reliably match 98.7% of the winning accounts from the fiche period to a PIN, implying a negligibly small rate of attrition. In practice, little variation in lottery prizes is lost by comparing winners of large prizes to winners of small prizes (typically 1,000 SEK in the PLS data) instead of comparing winners of large prizes to nonwinners. Because the majority of PLS prizes are small, the small prize winners can still be used to accurately estimate the counterfactual trajectories of large winners. Online Appendix III.F contains an illustration, based on hypothetical data, of the procedure used to generate the PLS cells.

II.B. The Kombi Lottery

Kombi is a monthly subscription ticket lottery whose proceeds are given to the Swedish Social Democratic Party and its youth movement. Participants are therefore unrepresentative of the Swedish population in terms of political ideology. Subscribers are billed monthly for their tickets. Ticket owners automatically participate in regular prize draws in which they can win cash prizes or merchandise.

Kombi provided us with an electronic data set with information about the monthly ticket balance of all Kombi participants since January 1998.⁶ They also provided a list of all individuals who won 1 million SEK (net of taxes) or more, along with information about the month and year of the win. Our empirical strategy is to compare each winner of a large prize with “matched controls” who did not win a large prize but owned an identical number of tickets at the time of the draw. We matched each winner of a large prize to (up to) 100 controls. To improve the precision of our estimates, we choose controls similar in age and sex whenever possible. In those cases in which we had fewer than 100 controls, we included all of them. Our final estimation sample includes the winners of 462 large prizes matched to 46,024 controls (comprising 40,366 unique individuals).

II.C. The Triss Lottery

Triss is a scratch-ticket lottery run since 1986 by Svenska Spel, the Swedish government–owned gambling operator. Triss tickets can be bought in virtually any Swedish store. Our sample contains winners of two types of Triss prizes: Triss-Lumpsum and Triss-Monthly.

Winners of the Triss-Lumpsum and Triss-Monthly prize are eligible to participate in a morning TV show broadcast on national television (“TV4 Morgon”). At the show, Triss-Lumpsum winners draw a prize from a stack of tickets. This stack of tickets is determined by a prize plan that is subject to occasional revisions. Triss-Lumpsum prizes vary in size from 50,000 to 5 million SEK (net of taxes). Triss-Monthly winners participate in the same TV show, but draw one ticket that determines the size of a monthly installment and a second that determines its duration. The tickets are drawn independently. The durations range from 10 to 50 years, and the monthly installments range from 10,000 to 50,000 SEK. To make the monthly installments in Triss-Monthly comparable to the lump-sum prizes in the other lotteries, we convert them to present value using a 2% annual discount rate.

Svenska Spel supplied us with a spreadsheet with information on all participants in Triss-Lumpsum and Triss-Monthly prize draws in the period between 1994 and 2010. The Triss-Monthly prize was not introduced until 1997. Around 25 Triss-Lumpsum prizes and five Triss-Monthly prizes are awarded each month. With the help of Statistics Sweden, we were able to use the information in the spreadsheet (name, age, region of residence, and often also the names of close relatives), to reliably identify the PINs of 98.7% of the winners of Triss prizes. The spreadsheet also notes instances in which the participant shared ownership of the ticket. Our main analyses are based exclusively on the 90% of winners who did not indicate prior to the TV show that they shared ownership of the lottery tickets. However, all of our main results are substantively identical with shared prizes included (see Online Appendix IV.D).

Our empirical strategy makes use of the fact that conditional on making it to the show, prizes are drawn randomly conditional on the prize plan. We assign players to the same cell if they won the same type of lottery prize (Triss-Lumpsum or Triss-Monthly) under the same prize plan and in the same year.

III.A. Inference

We took a number of steps to ensure the standard errors we report convey the precision of our estimates as accurately as possible. Throughout the article, we adjust the analytical standard errors for two sources of nonindependence. First, players who win more than one prize will typically appear more than once in the sample (as will the children of such players). Second, in the intergenerational analyses, siblings’ outcomes are clearly not independent. We therefore reported clustered standard errors (Liang and Zeger 1986) throughout the manuscript. We cluster at the level of the player in the adult analyses and at the household level in the intergenerational analyses (using an iterative process that always assigns half-siblings to the same cluster).

The analytical standard errors rely on an asymptotic approximation that may introduce substantial biases in finite samples. Though our sample size is large, some of the variables are heavily skewed, so standard rules of thumb about the appropriate sample sizes may not apply. To quantify the amount of finite-sample bias, we conducted Monte Carlo simulations in our adult and intergenerational estimation samples (see Online Appendix VII.A for details). In the simulations, we exploit the fact that the prizes are randomly assigned within cells to obtain the approximate finite-sample distribution of our test statistics under the null hypothesis that the effect of wealth is zero. Procedurally, we generated 1,000 data sets in which the prizes won by the players (and hence also their children) were permuted within each cell. For each outcome and each permuted sample, we then estimated equation (1).

In the simulated data, prize amount is (conditionally) independent of the outcome by construction, so if the p-values obtained from analytical standard errors follow a uniform distribution, we interpret this finding as evidence that they are reliable. By this criterion, the analytical standard errors we report in our main analyses are generally reliable. In all our major analyses, we nevertheless supplement analytical standard errors with resampling-based p-values (constructed from the resampling distribution generated in the Monte Carlo simulations). In some analyses of either skewed variables (e.g., prescription drug consumption) or rare binary variables (e.g., short-run cause-specific hospitalizations), we occasionally observe nontrivial differences between the analytical and resampling-based p-values. In such cases, we rely on the resampling-based p-values, which are usually more conservative.

III.B. Random Assignment

If the identifying assumptions of Table II are correct, no covariates determined before the lottery should have predictive power for the lottery outcome once we condition on the cell fixed effects. Normalizing the time of the lottery to 0, we test for (conditional) random assignment by running regressions of the following form: <mml:math display="block"><mml:mrow><mml:msub><mml:mi>P</mml:mi><mml:mrow><mml:mi>i</mml:mi><mml:mo>,</mml:mo><mml:mn>0</mml:mn></mml:mrow></mml:msub><mml:mo>=</mml:mo><mml:msub><mml:mi mathvariant="bold">X</mml:mi><mml:mrow><mml:mi>i</mml:mi><mml:mo>,</mml:mo><mml:mn>0</mml:mn></mml:mrow></mml:msub><mml:mi mathvariant="bold-italic">β</mml:mi><mml:mo>+</mml:mo><mml:msub><mml:mi mathvariant="bold">Z</mml:mi><mml:mrow><mml:mo>−</mml:mo><mml:mn>1</mml:mn></mml:mrow></mml:msub><mml:mi mathvariant="bold-italic">γ</mml:mi><mml:mo>+</mml:mo><mml:msub><mml:mi mathvariant="normal">ϵ</mml:mi><mml:mrow><mml:mi>i</mml:mi><mml:mo>,</mml:mo><mml:mn>0</mml:mn></mml:mrow></mml:msub><mml:mo>,</mml:mo></mml:mrow></mml:math>Pi,0=Xi,0β+Z−1γ+ϵi,0,(2) where P_i,0 is prize money at the time of the event, X_i,0 is the matrix of cell fixed effects, and Z_–1 is the full set of baseline controls (see Table I) measured at t = –1. To test for random assignment, in Table III we report omnibus p-values for joint significance of the demographic characteristics defined in Table I, the health characteristics, and their union. We run these randomization tests in the pooled adult sample, in the four lottery samples, and for parents of prelottery children or postlottery children. In the pooled sample, we also estimate equation (2) without cell fixed effects. Overall, the results in Table III are consistent with our null hypothesis that wealth is randomly assigned if and only if we condition on the cell fixed effects.⁸

Because the hypothesis of conditional random assignment of wealth is the least credible in the potentially selected sample of postlottery children, we also tested whether wealth shocks have an impact on fertility (a fundamental question in its own right—see Becker and Tomes 1976). As is common in studies of infant health, we restricted our analyses to postlottery children of female players. As shown in Online Appendix Table AIII, we find no evidence that lottery wealth affects fertility of women below the age of 50.

III.C. External Validity

In this section, we address a number of questions about the appropriateness of generalizing from our Swedish sample of lottery players to the Swedish population.

3. Is Lottery Wealth Different?

A general concern often voiced about studies of lottery winners is that people may react differently to lottery wealth than to other types of wealth shocks (e.g., changes in taxes, welfare systems, or asset-price fluctuations). This argument can take many specific forms, one of them being that lottery prizes are usually paid in lump sums, whereas many policy changes involve changes to income flows. Throughout the article, we test for heterogeneity by lottery and by type of prize (monthly installments versus lump sum). In interpreting these estimates, recall that the Triss-Monthly prizes supplement monthly incomes by 10,000 to 50,000 SEK ($1,400–7,000). Such figures are far too large to realistically replicate the features of most income support programs. Instead, they allow us to evaluate whether our conclusions about the effects of substantial shocks to permanent income are robust to the mode of payment. The informativeness of the estimates from the Triss-Monthly sample also varies across outcomes depending on the effective sample size.

According to a folk wisdom, lottery winners spend lottery wealth more frivolously than other types of wealth. In a companion paper on labor supply (Cesarini et al. 2015), we show that the earnings response to the lottery wealth shock is immediate, modest in size, seemingly permanent, and similar across lotteries. Figure I shows the trajectory of net wealth in the years following the lottery win. Plotted are coefficient estimates for t = –1, … ,10 obtained from our main estimating equation with the outcome variable defined as (household-level) year-end net wealth. In the year of the lottery, measured net wealth increases by over 60% of the prize amount won. The net wealth trajectories are similar across lotteries and suggest winners spread out the consumption of lottery wealth fairly evenly over time. The indications are thus that winners of large prizes in all lotteries enjoy a modest but sustained increase in consumption and leisure for an extended period of time.

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Figure I

The Effect of Lottery Wealth on Net Wealth According to Administrative Registers

See Online Appendix VI.D for details on the net wealth variable. Plotted in the figure are regression coefficients from equation (1) with the dependent variable defined as household net wealth at t = −1, …, 10. Standard errors are clustered by individual, and the error bars give 95% confidence intervals. The seemingly anomalous lottery-specific estimates (e.g., PLS at t = 0 and Kombi at t = 9) are all imprecisely estimated. For example, the t = 9 Kombi estimate is based on draws from a single year of data; the Kombi panel begins in 1998 and our last year with wealth data is 2007. Household wealth is defined as the wealth of the winner plus, if applicable, the wealth of the spouse or cohabitating partner. Coefficients can be interpreted as the effect of a 1 SEK increase in lottery prize on measured net wealth. Only the lump-sum lotteries are included in the total.

IV.A. Total and Cause-Specific Mortality

We begin with mortality because it is the most objective health measure available in our data. In our main analyses of mortality, the dependent variable is an indicator variable that takes the value 1 if the individual was deceased t = 1, … , 10 years after the lottery. For each of these 10 survival horizons, we estimate a separate linear probability model. In all lottery regressions, we control for the full set of baseline characteristics measured at t = –1 and scale the treatment variable so that a coefficient of 1.00 means 1M SEK decreases the survival probability over the relevant time horizon by 1 percentage point.

Given that wealth-mortality gradients are sometimes given causal interpretations, we compare the lottery-based estimates to the cross-sectional gradients estimated from nonexperimental variation in a Swedish representative sample drawn in 2000 and a U.S. sample. The U.S. analyses are based on all adult members of the Health and Retirement Study’s AHEAD cohort who were alive in 1993. To maximize comparability to the lottery estimates, we reweight both cross-sectional samples to match the age and sex distributions of the pooled lottery sample. We estimate Swedish cross-sectional gradients from regressions of the form <mml:math display="block"><mml:mrow><mml:msub><mml:mi>Y</mml:mi><mml:mrow><mml:mi>i</mml:mi><mml:mo>,</mml:mo><mml:mi>t</mml:mi></mml:mrow></mml:msub><mml:mo>=</mml:mo><mml:msub><mml:mi>α</mml:mi><mml:mi>t</mml:mi></mml:msub><mml:msub><mml:mi>W</mml:mi><mml:mrow><mml:mi>i</mml:mi><mml:mo>,</mml:mo><mml:mn>1999</mml:mn></mml:mrow></mml:msub><mml:mo>+</mml:mo><mml:msub><mml:mi mathvariant="bold">Z</mml:mi><mml:mrow><mml:mi>i</mml:mi><mml:mo>,</mml:mo><mml:mn>1999</mml:mn></mml:mrow></mml:msub><mml:msub><mml:mi mathvariant="bold-italic">γ</mml:mi><mml:mrow><mml:mi mathvariant="normal">t</mml:mi></mml:mrow></mml:msub><mml:mo>+</mml:mo><mml:msub><mml:mi mathvariant="normal">ϵ</mml:mi><mml:mi>i</mml:mi></mml:msub><mml:mo>,</mml:mo></mml:mrow></mml:math>Yi,t=αtWi,1999+Zi,1999γt+ϵi,(3) where Y_i,t is an indicator variable equal to 1 if individual i is deceased in year t, W_i,1999 is net wealth by December 31, 1999, and Z_i,1999 is a set of controls. We estimate a separate regression for t = 2001, … , 2010. The U.S. gradients are estimated using an analogous specification, except that covariates are measured in 1992, and mortality observed for t = 1994, … , 2003. We winsorize net wealth in both samples at the 1st and 99th percentiles and convert the winsorized variable to year 2010 SEK.

Figure II graphically illustrates the estimated coefficients in (i) our pooled lottery sample, (ii) the weighted Swedish representative sample controlling for just the birth demographics, (iii) the weighted Swedish sample controlling for the baseline characteristics, and (iv) the weighted U.S. sample with controls for birth demographics. The estimates for t = 2, 5, and 10 are reported in Online Appendix Table AVIII, which also shows the fraction of individuals deceased at t = 2, 5, and 10 in the lottery sample and the two representative samples.

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Figure II

Wealth and Mortality

This figure contrasts our lottery-based estimates of the effect of wealth on mortality to gradients estimated in Swedish and U.S. population samples. The population samples have been reweighted to match the sex and age distribution of our sample of lottery winners. Gradients are separately estimated with controls for birth demographics for Sweden and the United States, as well as with the full set of baseline controls for Sweden. Standard errors are clustered by individual, and the error bars give 95% confidence intervals of the coefficient.

The wealth-mortality gradients in Sweden and the United States are of similar magnitude and exhibit similar trajectories over time.¹² In Sweden, an additional 1M is associated with approximately a 2.8 percentage point decrease in 10-year mortality risk, and the point estimate only falls to 2.1 if we control for the full set of baseline characteristics (Online Appendix Table AVIII).

In sharp contrast to the cross-sectional gradients, the lottery-based estimates are close to zero and never statistically distinguishable from zero in the pooled sample. For all survival horizons greater than two years, the lottery-based estimates are statistically distinguishable from the gradients. For 10-year mortality, the 95% confidence interval allows us to rule out causal effects one sixth of the gradient. We find no evidence of a positive gradual accumulation of effects. If anything, the temporal pattern appears to be the opposite: positive effects fade to zero and may even be negative over longer horizons. The estimates and their standard errors are substantively identical if we use the probit estimator (Online Appendix Table AVIII), and our conclusions are robust to restricting the sample to lottery players who can be followed for at least 10 years after the lottery (thus holding the composition of the lottery sample fixed; see Online Appendix Figure AII).

We repeated the above analyses for all the common and hypotheses-based cause-specific mortalities at t = 5 and 10 (Online Appendix Figures AIII–AIV and Table AIX).¹³ We find no evidence that lottery wealth affects the probability of death due to any of these causes. Compared with the respective gradients, the lottery-based estimates almost always imply a smaller protective effect (or even a harmful effect) of wealth. Our lottery-based estimates are statistically distinguishable at the 5% level from several of the cause-specific 10-year mortality gradients: alcohol, circulatory disease, diabetes, ischemic heart disease, other, and respiratory disease.

To investigate if the small effects on overall mortality masks any heterogeneous effects, we conducted additional analyses in a number of subpopulations. Health is a stock whose correlation with income varies over the life cycle, and so may the mix of causal forces that give rise to the correlation at different ages (Smith 2007; Cutler, Lleras-Muney, and Vogl 2012). We therefore reran our main analyses of overall mortality at t = 2, 5, and 10 in three subsamples defined by age at the time of the lottery: early (ages 18–44), middle (45–69), and late adulthood (70 +). We also test for heterogeneity by sex, health status (hospitalized or not during the past five years), college completion, and income (individual disposable income above versus below the median in the individual’s age category). In each heterogeneity analysis, we estimated an extended version of equation (1) in which all coefficients are allowed to vary flexibly by subsample. We then conduct a conventional F-test of the null hypothesis that the effect of wealth is the same across all subgroups.

As shown in Online Appendix Figure AV and Online Appendix Tables AX–AXI, we find no strong evidence of heterogeneous effects, but we observe nominally significant effects of wealth on mortality in some of the subsamples; for example, we find signs that wealth increases 10-year mortality in players above 70 years of age, in female players, and in players with below-median income, and suggestive evidence that wealth is protective in individuals with college degrees. Given the large number of hypotheses tested, we interpret these results cautiously. The most important conclusion from our heterogeneity analysis is that in each of the 11 subsamples, some of which include fewer than 15% of the members of the pooled sample, the estimated effect of wealth on 10-year mortality is precise enough to rule out even the more conservatively estimated Swedish gradient of −2.1. In fact, we can reject causal effects one third as large as this gradient in 7 of our 11 subsamples, including in several populations (e.g., low-income households) sometimes identified as vulnerable in the literature.

We also investigated whether the effect of wealth on overall mortality varied by lottery (Online Appendix Table AXII). Because most players whom we can follow for 10 years are from the PLS lottery, the 10-year mortality estimates in remaining lotteries are too imprecise to convey any valuable information about heterogeneity. For two- and five-year mortality, the estimated effects are similar across the lotteries and estimated with reasonable precision. The cross-sectional gradient for five-year mortality is −1.57 controlling for birth demographics, a magnitude we can reject at the 5% level in all lotteries except Kombi (95% CI −1.85 to 2.50).

To better understand what sort of nonlinear effects are consistent with our results, we reestimated our main mortality regressions, dropping small (<10K), large (>2M), or very large (>4M) prizes altogether. These sample restrictions appear to have little systematic impact on our estimates, suggesting that none of our results are driven by extreme prizes (Online Appendix Table AXIII). We also estimated two piecewise linear models, the first with a single knot at 1M and the second with knots at 100K and 1M. If lottery wealth has positive and diminishing marginal health benefits (Adler and Newman 2002), we expect negative coefficients that are further away from zero at lower prizes. Our point estimates suggest the opposite pattern—increases in mortality risk that are greatest at lower levels of wealth. Online Appendix Figure AVI illustrates the spline estimates. Though we can never statistically reject constant marginal effects, the upper panel of the figure shows our 95% confidence intervals allow us to rule out even modest positive diminishing marginal effects of wealth. For example, according to the first model, the effect of a 1M wealth shock on 10-year survival probability is at most 0.2 percentage point. The lower panel shows the marginal effect of wealth below 100K is estimated with too little precision to convey useful information.

We supplement our main results with estimates from duration models, which make stronger parametric assumptions about the relationship between wealth and mortality but also accommodate the right-censoring of the data and thus make more efficient use of the full data set (which includes some players observed up to 24 years after the lottery event). We estimate an exponential proportional hazard model in which, again normalizing the time of the lottery to t = 0, the hazard of death individual i faces at t is assumed to be given by <mml:math display="block"><mml:mrow><mml:msub><mml:mi>h</mml:mi><mml:mi>i</mml:mi></mml:msub><mml:mrow><mml:mo stretchy="true">(</mml:mo><mml:mrow><mml:mi>t</mml:mi><mml:mo stretchy="false">|</mml:mo><mml:msub><mml:mi>P</mml:mi><mml:mrow><mml:mi>i</mml:mi><mml:mo>,</mml:mo><mml:mn>0</mml:mn></mml:mrow></mml:msub><mml:mo>,</mml:mo><mml:msub><mml:mi mathvariant="bold">X</mml:mi><mml:mi>i</mml:mi></mml:msub><mml:mo>,</mml:mo><mml:msub><mml:mi mathvariant="bold">Z</mml:mi><mml:mrow><mml:mi>i</mml:mi><mml:mo>,</mml:mo><mml:mo>−</mml:mo><mml:mn>1</mml:mn></mml:mrow></mml:msub></mml:mrow><mml:mo stretchy="true">)</mml:mo></mml:mrow><mml:mo>=</mml:mo><mml:mtext>exp</mml:mtext><mml:mo stretchy="true">(</mml:mo><mml:mstyle displaystyle="true"><mml:munderover><mml:mo>∑</mml:mo><mml:mrow><mml:mi>j</mml:mi><mml:mo>=</mml:mo><mml:mn>1</mml:mn></mml:mrow><mml:mn>3</mml:mn></mml:munderover><mml:mrow><mml:msub><mml:mi>γ</mml:mi><mml:mi>j</mml:mi></mml:msub><mml:msubsup><mml:mi>A</mml:mi><mml:mrow><mml:mi>i</mml:mi><mml:mi>t</mml:mi></mml:mrow><mml:mi>j</mml:mi></mml:msubsup></mml:mrow></mml:mstyle><mml:mo stretchy="true">)</mml:mo><mml:msub><mml:mi>λ</mml:mi><mml:mn>0</mml:mn></mml:msub><mml:mo>⁡</mml:mo><mml:mtext>exp</mml:mtext><mml:mrow><mml:mo stretchy="true">(</mml:mo><mml:mrow><mml:mi>α</mml:mi><mml:msub><mml:mi>P</mml:mi><mml:mrow><mml:mi>i</mml:mi><mml:mo>,</mml:mo><mml:mn>0</mml:mn></mml:mrow></mml:msub><mml:mo>+</mml:mo><mml:msub><mml:mi mathvariant="bold">X</mml:mi><mml:mi>i</mml:mi></mml:msub><mml:msub><mml:mo>,</mml:mo><mml:mn>0</mml:mn></mml:msub><mml:mi mathvariant="bold-italic">β</mml:mi><mml:mo>+</mml:mo><mml:msub><mml:mi mathvariant="bold">Z</mml:mi><mml:mrow><mml:mi>i</mml:mi><mml:mo>,</mml:mo><mml:mo>−</mml:mo><mml:mn>1</mml:mn></mml:mrow></mml:msub><mml:mi mathvariant="bold-italic">γ</mml:mi></mml:mrow><mml:mo stretchy="true">)</mml:mo></mml:mrow><mml:mo>,</mml:mo></mml:mrow></mml:math>hi(t|Pi,0,Xi,Zi,−1)=exp(∑j=13γjAitj)λ0⁡exp(αPi,0+Xi,0β+Zi,−1γ),(4) where P_i,0 is the lottery prize won at event time t = 0, A_it is the age (in years) of individual i at time t, X_i,0 is the vector of cell fixed effects, Z_i,–1 is the vector of predetermined covariates except for age, and λ₀ is the baseline hazard. Because we do not wish to impose the implausible restriction that individuals face a constant hazard of death over the life cycle, we allow the hazard to vary with a third-order polynomial in age. The key assumption in equation (4) is that all of the exponentiated covariates proportionally affect this age-varying baseline hazard. In Table VI, we report estimates of equation (4) obtained from the full adult sample and the subsamples used in the heterogeneity analyses above. The first column shows the estimated effect of wealth in the full sample. The estimates are all shown as hazard ratios, so the estimate in column (1) of 1.015 (95% CI 0.964–1.066) means the mortality risk increases by 1.5% for each million SEK won. The next two columns contains estimates from the reweighted Swedish 2000 representative sample. The hazard ratio is 0.874 with the baseline set of covariates and 0.828 with the narrower set of controls. In the cross section, 1M SEK of net wealth is thus associated with a 17.2% or 12.6% lower mortality risk. The results from the heterogeneity analyses are qualitatively similar to the OLS findings. Hazard ratios hover around 1.00 and are estimated with enough precision to reject the gradient in all subsamples except college-educated winners and winners aged 18–44.

As an alternative benchmark for these estimates, an extra year of schooling is believed to reduce mortality rates by about 8% across the entire life cycle (Deaton 2002, p. 21). Our estimates allow us to reject that 100,000 SEK—roughly the annual U.S. per pupil spending in high school—reduces the mortality rate by more than 0.4%. We also sought to evaluate whether the effects are small or large from a welfare perspective, by calculating the cost per life year saved at the bounds of our confidence intervals. Even if we take the lower bound of our 95% CI for the hazard, the estimated hazard translates into an average prolonged life of four months per 1M SEK in our sample. Our estimates therefore allow us to reject costs smaller than 3M SEK per year of life saved, approximately three times larger than a recent Swedish estimate of the value of a quality-adjusted life year of 1.2M SEK (Hultkrantz and Svensson 2012, p. 309).

IV.B. Health Care Utilization

We examine two types of health care utilization: hospitalizations requiring inpatient care and consumption of prescription drugs. The hospitalization analyses are based on data on inpatient care from the National Patient Register. From 1987 onward, this register contains information about each patient’s arrival and discharge dates and diagnoses codes (in ICD format). Our analyses of drug prescriptions are based on data from the Prescribed Drug Register, which contains information about all over-the-counter sales of prescribed medical drugs between 2006 and 2010. During this period, we observe on which day a prescription was purchased, the Anatomical Therapeutic Chemical Classification System (ATC) code of the drug, and the number of defined daily doses (DDDs) purchased. A DDD is an estimate of the maintenance dose per day of a drug when it is used for its main indication.

Unlike the well-studied wealth-mortality gradients, health care utilization gradients with respect to income are on average quite small, but vary both in their sign and their magnitude across countries (Majo and van Soest 2012). Given Sweden’s universal coverage, extrapolations of the findings reported here to other settings are clearly fraught with numerous difficulties. To facilitate the exposition, we seek to mimic the mortality analyses as closely as possible but relegate most of the findings to the Online Appendix. In our analyses of cause-specific hospitalizations, we consider the same common and hypotheses-based causes as in the mortality analyses. In our hospitalization analyses, the main outcome variables are a set of binary outcome variables equal to 1 if in at least one of the 2, 5, and 10 years following the lottery the individual was hospitalized for at least one night. We construct one variable for each of the specific causes and also an omnibus (all-cause) variable that includes hospitalizations due to all causes except pregnancy. We also construct an alternative all-cause hospitalization variable for hospitalizations whose duration exceeds at least one week. We also construct a health index that aggregates the information available in the registers to predict five-year mortality risk. The index, which ranges from 0 to 100, is defined so higher values denote worse health (see Online Appendix VI.C for details).

In our drug prescription analyses, the nature of the data required us to make some minor changes to the categories,¹⁴ the most important of which is that we include mental health as one of the hypotheses-based causes.¹⁵ We estimate the impact of wealth on the intensive- and extensive-margin drug consumption 2006–2010. Our primary outcome is the sum of DDDs prescribed between 2006 and 2010 in all drug categories except contraceptives.

In all health care utilization analyses, we restrict the estimation sample to individuals who were alive for the entire period over which a variable is defined. For example, the drug prescription analyses are restricted to a sample of individuals who won before 2006 (the first year for which we have data) and were alive in 2010 (the last year with data).

To give a broad summary of the overall pattern of results, Table VII reports results for eight key outcomes: all-cause hospitalizations and the health index at t = 2, 5, 10; total drug consumption; and intensive-margin consumption of mental health drugs. As a benchmark, the table also reports the wealth gradients estimated in a representative sample reweighted so its sex and age distribution matches the lottery sample.¹⁶ The causal estimates on the three all-cause hospitalization variables are not statistically distinguishable from zero. The estimated marginal effects of 1M SEK on the probability of hospitalization within 5 and 10 years are 0.39 (95% CI −0.82 to 1.60) and −0.03 percentage points (95% CI −1.54 to 1.48), respectively. Given baseline probabilities of 38.3% and 51.2%, these estimates allow us to rule out effects on relative risk that are fairly small. For t = 2 and t = 5 hospitalizations, the causal estimates are statistically distinguishable from the gradients at the 10% level.

The estimated effect of 1M on the health index, whose value ranges from 0 to 100, is −0.08 (95% CI −0.36 to 0.20) at t = 2, 0.30 (95% CI −0.23 to 0.82) at t = 5, and 0.45 (95% CI −0.24 to 1.15) at t = 10. These estimates are clearly statistically distinguishable from the gradients.

Our estimated effects on total and mental health drug consumption are also small. The 95% confidence interval for the estimated impact of 1M SEK on total drug consumption is −0.04 to 0.01 standard deviation units. For mental health, our estimate suggests wealth significantly reduces intensive margin consumption, but the coefficient estimate (−32.50) is small. In standard deviation units, 32.5 DDDs corresponds to an effect of 0.03, so the estimated effect is not an exception to the overall pattern of small effects of wealth. Moreover, mental health was one of several categories of prescription drugs considered, and the result does not survive a multiple-hypotheses correction that takes into account all the drug-prescription variables analyzed (adjusted p-value = .21).¹⁷ We therefore interpret the finding cautiously. In post hoc analyses reported in Online Appendix Table AXVI, we found that the effect, if real, is explained mostly by reductions in the consumption of anxiolytics (used to treat anxiety) and hypnotics and sedatives (used to treat insomnia). The mental health result shows up robustly if a count model is used in lieu of our baseline OLS specification, but the estimated effect is not statistically significant if we winsorize the mental health variable at the 99th percentile (Online Appendix Table AXVII).

For four of the outcomes in Table VII—five-year hospitalization, five-year health index, total drug consumption, and mental health drug consumption—we also undertook a series of additional heterogeneity and nonlinearity analyses analogous to those conducted for overall mortality (Online Appendix Tables AXIX-AXXII). The estimated effect on mental health is negative in 10 out of 11 subsamples considered in the heterogeneity analyses (the exception is individuals above 70) and in all four lotteries, and appears to be driven primarily by large-prize winners.

Online Appendix Table AXVIII reports lottery-based estimates and wealth gradients for the full set of cause-specific hospitalization variables we considered. For all but 2 of the 26 outcomes, the gradients are negative, implying higher net wealth is associated with lower hospitalization risk. The exceptions are 10-year hospitalization risk for cancer and cerebrovascular disease. The causal estimates also exceed the gradients for all but two outcomes, implying that the evidence in its entirety suggests that the causal benefits of wealth on health are of smaller magnitude than the gradient. However, the difference is only statistically significant at the 5% level for six outcomes: all-cause hospitalizations lasting at least a week (t = 5), alcohol (t = 5 and t = 10), diabetes (t = 5 and t = 10), and ischemic heart disease (t = 5). An analogous analysis of the drug prescription variables yields similar conclusions. For example, the estimated causal effects on the eight extensive margin drug variables are always greater than the gradients, though the difference is only significant for cerebrovascular disease and diabetes (Online Appendix Table AXIV).

V.A. Child Health

Table VIII summarizes the results for our 18 prespecified child health outcomes. For each outcome, we report lottery-based estimates alongside household-income gradients.

We begin with the analyses of infant health, which are based on variables derived from the Medical Birth Register. Columns (1)–(3) of Table VIII display the results for our three prespecified (and commonly studied) outcomes—birth weight (in grams), preterm birth (gestation length < 37 weeks), and low birth weight (birth weight < 2,500 grams). Whereas all remaining analyses are based on prelottery children, the infant health analyses are restricted to the smaller sample of postlottery children born to female players, leading to less precise estimates. None of the three causal estimates are robustly distinguishable from either zero or the household-income gradients.

We use data from the Swedish Conscript Register to construct three measures of body weight: BMI measured on a continuous scale and indicator variables for having a BMI above 25 and 30, the standard cutoffs used to define “overweight” and “obesity.” Conscription was mandatory for all Swedish men until 2010, so these analyses are limited to male prelottery children who reached conscription age (18–19) no later than 2010. The results from these analyses are shown in columns (4)–(6). For BMI, the point estimate is −0.11 with a 95% CI that ranges from −0.55 to 0.33 (-0.18 to 0.10 in standard deviation units). We estimate a statistically significant effect of wealth on obesity risk: according to our point estimate, 1M SEK reduces the probability of being obese around age 18 by 2.1 percentage points, roughly twice the size of the gradient. The obesity result survives an adjustment for multiple-hypothesis testing²¹ (adjusted p-value = .04), but because the estimated effect is outside the range we consider plausible and is not statistically significant in several of our sensitivity analyses, we interpret the result with some caution.²²

We also used data from the Prescribed Drug Register to study prescription drug consumption in four categories. The first three categories—asthma & allergy, mental health and ADHD—have featured prominently in the U.S. literature on child development (Currie 2009). The fourth category—total—includes all drug consumption except contraceptives and drugs included in the first three categories. The results from the prescription-drug analyses are shown in columns (7)–(10). We find no evidence that wealth impacts the total number of DDDs consumed in any of the four categories. The estimates consistently have good precision in the sense that we can bound the effect of 1M SEK to within ± 0.03 standard deviation units of the point estimate. The estimates are not statistically distinguishable from the household-income gradients.

Our final set of child health outcomes are hospitalization variables derived from the National Patient Register. We consider inpatient hospitalizations due to respiratory disease, external causes (accidents, injuries, and poisoning), and an omnibus (“all-cause”) category covering all hospitalizations except those due to pregnancy. For each category, we define indicator variables equal to 1 if a child was hospitalized due to that cause within two or five years of the lottery event. For the all-cause category, we also define a second set of indicators for hospitalizations lasting at least a week. We focus on respiratory disease and external causes because these are the most common chronic physical health conditions afflicting children in developed countries (Currie 2009).

The results of the hospitalization analyses are reported in columns (11)–(18) of Table VIII. According to our lottery estimates, a 1M SEK positive wealth shock increases the probability of all-cause hospitalization within two years by 2.1 percentage points and within five years by 3.4 percentage points. These estimates are statistically distinguishable both from zero and from the gradients, which are negative. The five-year effect surives an adjustment for multiple-hypothesis testing (following the same procedure as for obesity; adjusted p-value = .01). Expressed as relative risks, our estimates imply that 1M SEK increases both two- and five-year hospitalization risk by 19%. For hospitalizations due to both respiratory disease and external causes, the effects of wealth are of similar magnitude but less precisely estimated.

V.B. Child Development

Table IX reports results for our six development variables. Our first two outcomes, cognitive and noncognitive skills, are obtained from the Swedish Conscript Register and hence are available only for male children. Our remaining four variables measure scholastic achievement in ninth grade, the last year of compulsory schooling. Our primary outcome, obtained from the Ninth Grade Register, is the child’s overall GPA. From 2003, we also have information from the National Tests Register about performance on mandatory tests in Swedish, English, and mathematics. The six outcomes in Table IX have been normalized in a representative sample so that the effect size estimates can be interpreted in population standard deviation units.

Our measure of cognitive skills is the recruit’s score on a cognitive test similar to the Armed Forces Qualification Test. In addition to taking the test, recruits meet with a military psychologist who assesses their ability to deal with the psychological requirements of military service. The psychologist’s assessment is our measure of noncognitive skill. Previous work has shown it to be a reliable predictor of labor market outcomes even conditional on cognitive skills (Lindqvist and Vestman 2011). The estimated effect on cognitive skills is −0.11 standard deviation units and borderline significant (95% CI −0.21 to −0.02). The estimated effect on noncognitive skills is −0.03 standard deviation units (95% CI −0.19 to 0.12). For both outcomes, our estimates are clearly bounded away from the household-income gradients, which are 0.22 for cognitive skills and 0.16 for noncognitive skills.

The estimated effects on scholastic achievement, reported in columns (3)–(6), are also all negative, ranging from −0.02 standard deviation units for GPA to −0.08 standard deviation units for English. For GPA, our 95% CI is −0.08 to 0.03 standard deviation units. By way of comparison, the estimated household-income gradient is 0.26. We can thus reject causal effects far smaller than the gradient. The same conclusion holds for test scores in Swedish (95% CI −0.11 to 0.04 standard deviation units), English (95% CI −0.17 to 0.00 standard deviation units), and mathematics (95% CI −0.13 to 0.07 standard deviation units).

V.C. Robustness and Heterogeneity

We conducted a number of follow-up analyses of the findings in Tables VIII and IX. To simplify the exposition, we restrict these analyses to 15 variables: 9 key health outcomes and the 6 developmental outcomes. We relegate most results to the Online Appendix. Our discussion here is selective and seeks to accomplish two primary aims, the first of which is to evaluate the robustness and heterogeneity of the two effects that survived multiple-hypothesis correction: obesity and five-year all-cause hospitalizations (hereafter, “hospitalization”).

Online Appendix Table AXXIV shows that the effect size estimates for obesity and hospitalization do not change appreciably if the treatment variable is instead defined as the prize per child, although the obesity effect is no longer statistically significant. In our nonlinearity analyses (Online Appendix Table AXXV), we find that the estimated effect on hospitalization is of similar magnitude when we drop small (<10K), large (>2M), and very large prizes (>4M) prizes, whereas the obesity coefficient falls by 30–40% with the largest prizes dropped. In our main heterogeneity analyses, we stratified the sample by: (i) household-income (bottom quartile versus top three quartiles), (ii) child age at the time of the lottery (above or below nine), (iii) winning parent (father or mother), and (iv) child’s sex (male or female). In all eight subsamples, wealth is estimated to increase hospitalization risk, significantly so in six cases (Online Appendix Tables AXXVII–AXXVIII). The estimated effects on obesity are also directionally consistent across all the heterogeneity analyses and statistically significant in two subsamples: low-income households and households where the mother won. Overall, these analyses suggest that the hospitalization effect shows up robustly across specifications, whereas the obesity findings are less definitive.

The second aim is to systematically compare the causal effect estimates obtained from our eight subsamples to the household-income gradient. For the six developmental outcomes, we conducted a total of 44 heterogeneity analyses: 8 for each of the four scholastic achievement variables, and 6 for each of the two skills variables (only available in males, making sex-stratified analyses impossible). Of the 44 estimated treatment effects, all but 2 are statistically distinguishable from the population gradients at the 5% level,²³ and 7 are statistically distinguishable from zero at the 5% level, always with estimates implying adverse effects on developmental outcomes. The difference between the causal estimates and the household-income gradients is especially striking for GPA, where our 95% CIs allow us to reject positive effects one third as large as the household-income gradients in all eight subsamples. For health, the overall pattern of results is very different: our lottery-based estimates are typically not distinguishable from the household-income gradients. The only major exception is our hospitalization variable, for which we can reject the household-income gradient in all eight subsamples.²⁴

V.D. Comparison to Previous Causal Estimates

As a complementary benchmark for our estimates, we compared them to the range of effect sizes reported in meta-analyses of the causal impact of income on child outcomes (Duncan, Morris, and Rodrigues 2011; Cooper and Stewart 2013). These studies measure effects in units of standard deviations of the outcome per $1,000 of annual income. Using this scale, Cooper and Stewart (2013) reported positive effects in the range of 0.04–0.22 for studies finding effects on skills and scholastic achievement (of the 21 studies that satisfied the inclusion criteria in their study and examined cognitive/scholastic outcomes, 16 reported positive effects and 5 reported null results). The meta-analysis of Duncan, Morris, and Rodrigues (2011) was restricted to welfare-to-work experiments and reported an effect size range of 0.04–0.05 for cognitive skills.²⁵ It is noteworthy that even in the studies reporting positive effects at the lower end of these effect size ranges, the causal estimates exceed the income gradients.²⁶

There is no unassailable way of making our estimates comparable to those in previous studies. We proceed by measuring the shock to annual income as the annual payout that each lottery prize would generate if it were annuitized over a 20-year period at an actuarially fair price and a real return of 2.3%.²⁷ For point of reference, 1M SEK thus annuitized corresponds to an annual income increase of $8,800. A sustained increase in net annual income of that magnitude is large enough to move most households two to three deciles up the distribution of permanent income. Because the households in our sample enjoy an increase in income that lasts longer than the income supplements studied in previous quasi-experimental or experimental studies, our rescaled estimates will, all else equal, overstate the benefits of wealth in Sweden if the effects of income are positive and cumulative.

In all eight subsamples, we can rule out wealth effects on GPA smaller than 0.01 standard deviations, one quarter as large as the effects at the bottom end of the range reported in earlier studies with positive findings. To illustrate, Figure III plots our estimates, rescaled as described, of the causal effects on GPA from our pooled sample and four subsamples. To illustrate the point that the effect sizes in most published quasi-experimental studies exceed the gradient, the household-income gradient is depicted on the far left of the graph.²⁸ Replacing GPA in Figure III by any of the other five developmental outcomes gives substantively identical results.

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Figure III

Household Income and Child Grade Point Average

This figure compares our lottery-based estimates, rescaled for comparability, of the causal impact of wealth on child GPA in different subsamples to the household-income gradient estimated in a large representative sample of children. All coefficients are in standardized GPA units. Gradients include controls for birth demographics and the lottery estimates additionally include demographic controls for the winning parent. Standard errors are clustered using an iterative algorithm that assigns siblings and half-siblings to the same cluster.

Cooper and Stewart’s meta-analysis also covers physical and mental health outcomes. For these, effect sizes in studies with positive findings always exceed 0.03 standard deviation units (but are usually much larger). There are several reasons this lower bound may be a less informative benchmark for our health estimates than the corresponding lower bound for our developmental outcomes. The studies of health are fewer and tend to focus on outcomes whose comparability with our outcomes is more limited. Also, the tendency for health gradients to be smaller in Sweden (Online Appendix Figure AVIII), perhaps due to features of the Swedish health care system, may exacerbate concerns about external validity. With these caveats in mind, it is nevertheless interesting to note that our rescaled effect size estimates for the health outcomes studied in pre-lottery children consistently allow us to reject effects far below 0.03 standard deviation units.²⁹ Online Appendix Figure AVIII provides a graphical illustration for the nine key health outcomes considered in our follow-up analyses. For total drug consumption, we can for example rule out effects with an absolute value above 0.004 standard deviation units.

Considered in their entirety, our results clearly show that the marginal effects implied by our estimates are substantially smaller than previously reported causal estimates. Although heterogeneity in the outcome measures considered could explain why we consistently find smaller effects on health, this explanation is not credible for the developmental outcomes, where we use variables similar to those studied in most earlier work. There are several plausible reasons, none of them mutually exlusive, that may help explain why we systematically find smaller effects.

A first possible reason is population heterogeneity; most studies have focused on children from disadvantaged backgrounds, often in countries that differ in important ways from Sweden. Yet our estimates allow us to reject positive effects greater than 0.03 standard deviation units for outcomes such as drug consumption and school achievement even when we restrict our subsample to low-income households. For the two skills variables, we can rule out positive effects altogether in our low-income sample. Our estimates are also smaller than the positive effects found for some child health and development outcomes in quasi-experimental studies in Canada and Norway, two countries that share many institutional features with Sweden (Milligan and Stabile 2011; Løken, Mogstad, and Wiswall 2012).

Another potential source of the difference is that most policy changes or welfare-to-work experiments that have been exploited in earlier studies of income effects involve change to both incomes and prices (e.g., through changes to taxes or child care subsidies). Some authors have argued that these studies cannot credibly separate income effects from other changes and may be picking up difficult-to-model substitution effects (Currie 2009; Mayer 2010; Heckman and Mosso 2014).³⁰ Our estimates, by contrast, can be interpreted quite unambiguously as income effects. Finally, most earlier studies have evaluated the consequences of more modestly sized (usually monthly) income supplements. One of our lotteries (Triss-Monthly) pays prizes in monthly supplements, but the supplements are much larger than those considered in previous studies of income support programs. For some child outcomes, such as GPA, we continue to be able to rule out effects of $1,000 in annual income larger than 0.05 standard deviation units even when we restrict the sample to Triss-Monthly. The lower effects we report could reflect diminishing marginal effects of income supplements.

V.E. Parental Behavior

Even absent any direct evidence of an impact of wealth on most of our child outcomes, knowing if the wealth shocks have any discernible impact on parental behaviors is valuable. No variables in administrative records can be unambiguously interpreted as measures of parental investments or parenting quality, but our analysis plan (Cesarini et al. 2014) specified five outcomes that may be of some relevance for testing theories of how wealth impacts children’s outcomes. These five variables are asset transfers, local school quality, parental mental health, maternal smoking, and duration of parental leave.³¹ A summary of the results is that none of the causal estimates are statistically distinguishable from zero (see Online Appendix Table AXXIX for the full set of results). For three of the outcomes—duration of maternal leave, paternal leave, and school quality—we consider the estimates precise enough to conclude that the behavioral responses on these margins must be very small. For example, we can reject positive effects of 1M SEK on maternity leave larger than 13 days, a small effect given that the average mother claims 386 days of maternity leave benefits.