Florian Hoffmann. September - December Vancouver School of Economics University of British Columbia

Transcription

1 Lecture Notes on Graduate Labor Economics Section 1a: The Neoclassical Model of Labor Supply - Static Formulation Copyright: Florian Hoffmann Please do not Circulate Florian Hoffmann Vancouver School of Economics University of ritish Columbia September - December

2 1 Introduction In this section we study static and dynamic labor supply models. We treat the static version as a starting point only as it is ultimately too restrictive. We also take it as an opportunity to cover the Differencein-Difference research design (DiD), one of the empirical designs often used in the program evaluation literature (besides Regression Discontinuity designs (RD) and IV). It is therefore a good time for you to get an overview of these empirical methods by reading the Angrist-Krueger chapter in the Handbook of Labor Economics, the Lee-Lemieux-paper in the JEL, and the ertrand-duflo-mullainathan-paper in the QJE. 2 Static Labor Supply The static labor supply model is an application of standard micro-economic consumer theory. The household solves the following problem: max C,l U(C, l) (1) s.t. C w h + Y h = H l C, l 0, where C, l, h are consumption, leisure and hours of work, respectively, w is the wage rate, Y is non-labor income, and H is the time endowment (e.g. 24 hours per day). Note that the budget constraint can be re-written as C +w l w H +Y. This clarifies (a) that we have normalized the price of the consumption good to 1 (i.e. C is the Numeraire), (b) that the wage w can be interpreted as the (relative) price of leisure, and (c) that this relative price enters both sides of the budget constraint. Point (c) is what differentiates this model from the standard 2-goods household consumption model in which prices enter the expenditure side of the constraint only. Usually, one imposes the assumptions on preferences that U C as C 0, where U C is the marginal utility of consumption, and that preferences are non-satiated. The first assumption assures that C > 0 at the optimum, and the second assumption assures that the constraint holds with = instead of <. We do not want to impose assumptions on the marginal utility of leisure other than that it is positive since one frequently observes corner solutions for leisure, e.g. non-participation or unemployment, in the data. At an interior solution, the marginal rate of substitution between leisure and consumption is equal to the wage rate: U C (C, l ) w = U l (C, l ). The reservation wage is defined by the wage rate that makes the worker indifferent between a small unit of time and not working at all, i.e. w R = U l(c,h) U C (C,H). If w < w R the 1

3 tangency condition for an optimum cannot be satisfied, and the workers chooses a corner solution, where U C (C, l ) w < U l (C, l ). In the labor literature, especially in Macro-Labor, one often refers to the decision about how many hours to work given participation as the labor supply decision on the intensive margin and the decision whether to participate as the labor supply decision on the extensive margin. Of particular importance in the empirical literature is the labor supply elasticity, which is a unit-free measure of the slope of the labor supply curve. To apply the language of household theory, one usually reformulates the problem in terms of leisure demand rather than labor supply. The compensated labor supply elasticity is minus the elasticity associated with the Hicksian leisure demand curve, while the uncompensated labor supply elasticity is minus the elasticity associated with the Marshallian leisure demand curve. Totally differentiating the first-order condition for an interior solution with respect to wage and leisure, one gets: dl dw = Uc (w U CC U lc ) l + (w U CC U lc ) H = U ll (U lc U Cl ) w + w 2 U CC. (2) Using the second-order condition for a maximum together with the concavity of U(C, l) one can show that < 0. The slope of the leisure demand function has three components: The first term, Uc, is negative and represents the substitution effect. An increase in the wage rate raises the price of leisure, thus making the worker substitute towards work. The second term, (w U CC U lc ) l, is the conventional income effect. An increase in the wage rate makes leisure more expensive, and thus makes the budget set smaller. Throughout we assume that leisure is a normal good, so that the income effect of an increase in the price of leisure is negative. This imposes restrictions on preferences, particularly w U CC U lc < 0.T he third term, (w U CC U lc ) H, is the endowment effect. This is an additional income effect that does not exist in the conventional microeconomic model of consumption choice. The endowment effect exists in the static labor supply model because the wage rate, i.e. the price of leisure, enters both, the right-hand side and the left-hand side of the budget constraint. An increase in the wage rate does not only increase the relative price of leisure, but it also increases the value of the time endowment, w H. Given the assumption that leisure is a normal good, the endowment effect is positive, and it outweighs the income effect since H l. As a consequence, dl dw can be positive or negative. Likewise, dh dw - the slope of the labor supply function - can be positive or negative. From this, one can calculate the uncompensated labor supply elasticity η h,w = ( ) ( dh dw w ) h d log(h) d log(w). The ambiguity of dl dw is empirically unsatisfying because as long as we are unable to estimate subsitution effects or we are unwilling to make explicit assumptions about preference parameters, the model does not 2

4 impose any strong restrictions on the data. However, at the point of non-participation where l = H and w = w R, the equation above reduces to dl dw = Uc, and there is only a substitution effect. Hence, if the wage rate increases, for example because of an economic boom that puts pressure on wages, or because of a decrease in a labor tax, labor force participation is predicted to increase. This is a sharp prediction that is tested by Eissa and Liebman (1996), discussed below. It is worth pointing out an issue that has gained a lot of attention in recent research, both in microand labor-macro. When we talk about demand elasticities we usually think of unit-free measure of the change in quantity demanded in reaction to a change in the price, conditional on a strictly positive quantity demanded before and after the change. This is because most of us are used to models in which we impose restrictions on preferences that rule out corner solutions. However, when thinking about labor supply, corner solutions, that is non-participation, are a key empirical fact and cannot be ignored. The labor supply (or leisure demand) elasticity η h,w defined above does exactly that. It conditions on participation before and after the marginal wage change. We therefore call it the labor supply elasticity at the intensive margin or, following the Chetty et al. QJE paper (2011), the micro-elasticity of labor supply. ut when thinking about policy changes targeting labor supply, we also need to know the effect on labor force participation. That is, we also need to know how the labor force participation rate changes in response to a change in the wage rate net of taxes. In fact, this margin of labor supply is very often at the heart of public policy reforms. Unfortunately, the labor supply elasticity at the extensive margin is inherently undefined. This is because the derivative of the labor supply function is likely to be undefined at l = H. There are two different ways to address this problem, and both of them involve aggregation. The first way is to focus on the elasticity of the average hours worked in the economy, nowadays referred to as the macro-elasticity of labor supply. Another way is to study the elasticity of the labor force participation rate, which is what most people in the literature on intertemporal labor supply do. Notice at this point that we should expect, from the theory discussed above, that the labor supply elasticity at the extensive margin, however we define it, is larger than the micro-elasticity. 2.1 Eissa and Liebman (QJE, 1996) This paper is an early application of a quasi-experimental research design to the estimation of labor supply elasticities. Angrist and Krueger s chapter in the Handbook of Labor Economics and chapter 25 in Cameron and Trivedi (2005) provide an overview of the econometric methods used in this literature, which are Difference-in-Difference, Instrumental Variables, and Regression Discontinuity designs. DiD-strategies are simple panel-data methods applied to group means in cases where certain groups are exposed to the causing variable of interest and others are not. In empirical applications, the causing variable is a binary "treatment" variable that separates the sample into a group that is "treated" by some policy and another group that is not. The approach is well suited for estimating the effect of sharp 3

5 changes in the economic environment or changes in government policy when a suitable control group can be found. The work "changes" is crucial here because we need to be able to make before-after comparisons for treatment and control group. Eissa and Liebman examine the impact of the US Tax Reform Act of 1986 on labor supply. The questions being asked are: What were the effects on labor supply? Are they consistent with the basic model of labor supply? Part of the reform increased an existing earned income tax-credit (EITC) for single women with children. The original EITC works roughly the following way: The full credit is phased in at a 11% rate over the first $5000 of income which represents a subsidy to the household that increases in hours worked. The maximum credit is $550 until $6500 is reached, and is phased out at a rate of 12.2% up to earnings of $11,000 at which point the subsidy is exactly zero.the 1987 act increased the subsidy phase-in rate to 14% and decreased the phase-out rate to 10%. oth changes cause income and subsitution effects. Under the new reform those with incomes between $11,000 and $15,432 received a subsidy. The tax reform also raised non-work related deductions for households with and without children which shifts the budget line up and generates a pure income effect. This is problematic for policy analysis since it is hard to disentangle the labor supply effects of the different policy reforms, though Eissa and Liebman address this issue by using the fact that the former affects only low-income households with children while the latter potentially affects all groups in the labor force. The EITC reform has a sharp prediction on participation rates: Since it increases the effective wage rate, it generates an extra incentive to work - a pure subsitution effect - which in turn implies that participation rates should go up. At the same time it does not generate strong predictions about changes in hours of work conditional on participation since the policy generates income and subsitution effects. The DiD-strategy works as follows: Let Y be the observed outcome for individual i from group g at time t and let D gt be a dummy variable that is equal to one if group g is "treated" in period t by the reform and zero otherwise. In Eissa and Liebman, Y is a participation dummy in one specification and hours of work in the other specification. In their paper they use a Probit model for the first outcome, but for expositional simplicity we assume that they use a linear probability model. The assumption of the DiD-estimator is that outcomes are given by Y = βd gt + µ g + φ t + ε (3) where µ g is a group fixed effect, φ t is a time fixed effect, and ε is a standard OLS-error. Clearly β - the labor supply effect of the policy reform - can only be identified if D gt is not perfectly collinear with either of the fixed effects. With two periods and two groups this means that D gt must affect exactly one group in exactly one period. In other words, we need a group that is not affected by the policy change at all, serving as the control group and representing the counterfactual behavior if the reform had not happened, and a group that is affected by the policy reform and for which we can observe pre-reform outcomes (called 4

6 the treatment group or experimental group). Indexing the two periods and two groups by {1, 2} and assuming that D 22 = 1 but D 11 = D 12 = D 21 = 0 we get (under the usual OLS-assumption that ε is independent from the conditioning variables): β = (E [Y g = 2, t = 2] E [Y g = 2, t = 1]) (E [Y g = 1, t = 2] E [Y g = 1, t = 1]). (4) The empirical counterpart replaces the theoretical (population) moments by sample analogues. Using an upper bar for sample averages, we get the following estimator: β DiD = ( ) ( ) Y 22 Y 21 Y 12 Y 11. (5) Think about the interpretation of this estimator: The term in the first bracket is the difference in average outcomes for the treatment group before and after treatment, and the second term is the difference in average outcomes for the control group in the first and second period. Hence, the estimated average treatment effect β is the difference between these two differences - hence the name DiD. This is essentially a trend comparison between the two groups: Any differences in trends between the two groups is allocated to the estimate of the treatment effect. The underlying econometric assumption (other than linearity) can be seen from equation (3): The specification allows for a flexible time trend φ t, but this time trend is assumed to be the same for both groups in the absence of treatment. In empirical applications, this is the assumption to be justified. If there is evidence that the treatment and control group face different long-run trends in outcomes, this assumption fails, and β will be a biased estimate. A simple test is to see if the trends between the two groups were the same before the intervention, requiring data that record outcomes for several periods, not only one period, before the policy is implemented. To implement the DiD-estimator, one needs to choose a control group. In Eissa and Liebman, D gt is one after the EITC reform for individuals who are affected by it. These are low-income individuals with children. ut low-income individuals without children are not affected by the policy change and are thus a natural control group. Eissa and Liebman focus on single females. They first show that the average characteristics, such as education and age, are quite different between single women with and without children. This raises the question whether the identification assumptions are valid: Are these groups really likely to experience the same time shocks? One way to address this is to introduce additional controls into (3). Eissa and Liebman use a different approach and split the results by education group. They find that labor force participation rates for the treatment group increases by up to 4 percent relative to the control group. This is consistent with our simple model above since at the extensive margin there is only a substitution effect. At the same time, there is no significant response in annual hours and annual weeks worked which implies that the subsitution effect is close to the income effect. This result got a lot of attention. 5

7 It is important to keep in mind the limitations of the reduced-form approach in Eissa-Liebman. Most importantly, equation (3) implies that the agents in the model are myopic since no variables with timeleads and -lags enter the equation. ut it is reasonable to assume that individuals are at least to some extent forward looking and might adjust their behavior even before the policy intervention, which does not show up in the equation at all. On the other hand, they might smooth out their behavioral adjustment after the policy intervention, so a comparison of the behavior exactly before and after the intervention might not reflect the dynamic behavior of individuals. As we will see from the Intertemporal Labor Supply model, the way how individuals adjust to the policy intervention depends on whether it is anticipated and whether it is seen as a permanent or transitory shock to wages. The simple DiD-estimator does not make such a distinction. There is also an issue with external validity: Since the estimated parameters are not structural, they do not identify behavioral rules that are stable with respect to policy changes. Hence, the Eissa-Liebman results cannot be used to predict the effects of policy changes that lie outside of their sample. 2.2 Some Practical Issues with DiD-estimators It is clear from (4) that the average treatment effect β can be estimated using simple comparisons of sample averages. One only needs to compute averages for 4 different cells - the treatment and the control groups before and after the policy interventions. This is how the estimator is implemented and documented in Eissa and Liebman. Oftentimes however DiD is implemented by running an individual-level regression for (3). This is the more flexible approach since one can easily introduce other (continuous) control variables and since one can impose additional structure on the unobserved component ε. Furthermore, it potentially allows one to study heterogeneity in the treatment effect. However, there is a major problem with it which has caught a lot of attention at the beginning of the 2000 s: The OLS estimator of (3) will treat the estimation exercise as if there were a lot of individual-level observations indexed by, and this will yield potentially small standard errors. ut as (4) highlights, β is identified from only 4 aggregate observations. The OLS estimator on the individual level data will do this aggregation for us by the mechanics of OLS - after all, OLS estimates linearized conditional expectation functions, and the conditioning variables in (3) vary on the gt level only (i.e. there is only variation in the explanatory variables across groups and time, but not across individuals within group-time cells). The problem then is that the common iid-assumption for ε is likely to be invalid: Within groups (in Eissa and Liebman: Single Females with and without children), the errors are likely to be highly correlated. Note that this is not a problem of heteroscedasticity, so simple Huber-White heteroscedasticity-robust standard errors you know from basic econometrics won t help. This is a problem of serial correlation within groups that can yield much higher standard errors than without a correction. The solution is what is know as cluster-robust standard errors. See for example etrand, Duflo and Mullainathan (Quarterly Journal of Economics, 2003) for a Monte-Carlo 6

8 exercise documenting the serious problem with DiD-estimators when standard errors are not clustered. This is a problem that you are very likely to encounter in empirical research, so you should read that paper and the corresponding chapter in Cameron and Trivedi (2005). Stata now has a built-in routine for clustered standard errors, but you should understand the underlying econometric problem that motivates these corrections. Lets briefly go over the mechanics of the robust standard errors. Denoting the vector of the right handside variables in equation (3) by x and the vector of coeffi cients by γ the Huber-White heteroscedasticityrobust standard errors are given by the "sandwich"-estimator V [ γ x ] = x x 1 ε 2 x x x x 1 (6) = (X X) 1 X ΩX (X X) 1 (7) where ε = Y γ x and Ω is the variance-covariance matrix of ε. Remember from basic econometrics that the prime innovation of Huber and White is that to compute V [ γ x ] one does not need to estimate the high-dimensional Ω but only the lower-dimensional term X ΩX. The consistent estimator ( is given by ε2 x x ). If ε is assumed to be iid with variance σ 2 ε we get V [ γ x ] = σ 2 ε (X X) 1. However, as noted above, clustering is not a problem of heteroscedasticity but of serial correlation of ε within groups. Suppose we assume that ε is correlated within groups g and stack observations within groups to get Y g = γ X g + ε g where each vector/matrix in this equation has a length that is equal to the number of observations within cell. The cluster-robust standard errors are given by ( 1 ( ) ( 1 V clust [ γ x ] = x g x g) x g ε g ε g x g x g x g) (8) g g where ε g = Y g γ X g. Note that ε g ε g is a matrix that does not collapse to a diagonal matrix with elements ε 2! This is because we allow errors to be correlated arbitrarily within clusters, while Huber-White standard errors assume that errors are heteroscedastic but uncorrelated. In other words, Huber-White assume that Ω is diagonal, while clustered standard errors assume that Ω is block-diagonal, where each block is associated with a group. It is not always clear on which level to cluster. Here it seems reasonable that unobserved characteristics of single women with (or without) children are correlated across individuals and time. Thus, clustering on the group-level g seems to be appropriate. We could also assume that unobserved characteristics are iid over time in which case the level of clustering is gt, but this seems to be too restrictive. 7 g

9 Another approach some actually prefer is to aggregate the data up to the group-time level and run a regression on these data. Without control variables there are only 4 observations and the estimator is mechanically the same as a simple comparison of means like (4). One caveat with this approach is that one needs to weigh the data: Each cell computed during aggregation has potentially a different number of observations. Without weighing, each cell will be treated the same, even if there are cells with very few observations. For example, if there are very few single women with children in the second period in Eissa and Liebman, but many single women without children, the second group should be weighed more heavily in the estimation. Weighted regressions were the weights are the number of observations per cell can be implemented in Stata using the "aweight"-option. 8