ABSTRACT
How effective is the minimum wage at raising nondurable household consumption through the redistribution of income towards low-wage workers? To address this question, I use novel data on retail sales by county and exploit variation in the minimum wage rate across the United States and over time. I find that a 10 percent increase in the minimum wage raises sales by 0.6 percent in nominal terms and 0.4 percent in real terms. These large effects are suggestive of high marginal propensities to spend on nondurables out of minimum wage hikes. The expenditure response emerges even when exploiting only within-state variation.
I. Introduction
The minimum wage is a controversial policy in the United States. Many studies have explored the effects of the minimum wage on labor market outcomes, such as employment and wages. However, if the goal of this policy is to raise the level of household well-being, we should evaluate it based primarily on its effects on consumption, rather than on labor market outcomes alone. As Organisation for Economic Co-operation and Development (2013) notes, a working definition of well-being should involve the satisfaction of needs and wants, which is ultimately achieved through the consumption of goods and services, along with other inputs, such as time. Due to data limitations, examining an individual household’s consumption response to a change in the minimum wage is challenging. However, using aggregate data one can measure the response of aggregate consumption, at least for nondurables, where adjustment costs are low and the response of households is likely to be immediate.
I use a novel data set on the retail sales of groceries to produce a high-frequency measure of nondurable consumption at the county level. While the evolution of retail sales is similar to the national accounts measure of nondurable consumption at the state level, data on retail sales offer three key advantages for this study. First, retail sales data are available at a higher frequency than other geographically disaggregated data. I set the frequency to be a quarter, which allows for a precise identification of the timing in which the policy is implemented. Second, retail sales data are available at a highly disaggregated geographic level, which allows me to control for local economic conditions in a comprehensive way. Third, the heterogeneity in how tightly the minimum wage binds across U.S. counties, with some counties having more minimum wage workers than others, can be exploited to assess the differential effect of the policy. This further enhances the credibility of my identification strategy.
I find hikes in the minimum wage raise aggregate expenditure substantially. An increase of 10 percent in the minimum wage rate increases nominal sales by 0.6 percent and real sales by 0.4 percent. Higher prices account for a third of the increased expenditure, as nominal sales respond more than real sales. The magnitude of the estimated response is large. For comparison, the mean annual real nondurable consumption growth between 1959 and 2018 was 2 percent. Furthermore, the response is greater in counties where the minimum wage binds more tightly.
The large magnitude of my estimate of the expenditure response appears plausible and suggestive of high marginal propensities to spend on nondurable goods out of the additional income from minimum wage hikes. If the minimum wage had been raised to $10.10 from the rates prevailing at the end of my sample, nominal sales would have risen by $48 billion, $14 billion of which would have been explained by higher prices.1 The remaining $33 billion appears roughly consistent with the predicted increase in labor income for low-wage workers (Congressional Budget Office 2014). A high marginal propensity to spend out of a minimum wage hike could be reasonable given that in nominal terms it represents a permanent shock, it could expand borrowing limits, and it benefits workers likely to be financially constrained.2 In terms of the composition of the expenditure bundle, while some categories of nondurable goods are less likely to grow as much as the retail sales considered here (for example, alcohol and gasoline), services such as food away from home could (Cooper, Luengo-Prado, and Parker 2020). Additionally, other studies have found services other than food away from home do not seem to respond to minimum wage hikes, and durable goods increase only for a small group of households (Cooper, Luengo-Prado, and Parker 2020; Aaronson, Agarwal, and French 2012).
My identification strategy relies on the assumption that counties where the minimum wage rate rose would have experienced the same increase in sales that was observed in counties where the rate was unchanged, conditional on observable economic conditions and a county-specific average growth rate. I exploit the wide dispersion of county-level minimum wage rates across the country and over time during the period 2006–2014, which is mostly driven by states setting their own rates. I use a panel data research design in first differences with time and county fixed effects and controls for local economic conditions. In this setting, county fixed effects capture any static heterogeneity at the local level affecting the growth rate of sales, whereas time fixed effects absorb the common time trend. Additionally, variables such as employment and house prices at the county level allow me to control for local economic conditions, which is particularly important in the context of the Great Recession because not all counties experienced the crisis at the same pace and severity, and both could be correlated with policy changes.
I estimate a strong expenditure response to minimum wage hikes even when exploiting only within-state variation. Because my data are at the county level, I can perform a difference-in-difference-in-difference exercise by exploiting the fact that counties with higher shares of low-income households are likely to be more affected by the minimum wage. I interact the minimum wage with the share of low-income households in the county and introduce state-by-period fixed effects. This relaxes the identification assumption as it richly controls for state-level economic conditions and even allows for the state minimum wage to be chosen endogenously as long as such choice is driven by average conditions in the state and not by those of individual counties.
Several additional checks confirm the robustness of my results. First, the expenditure response to the minimum wage is concentrated in the first quarter after the hike is enacted. Second, my results are robust to unobservable spatial heterogeneity in time trends (Dube, Lester, and Reich 2010). Third, the response is not driven by states indexing their minimum wage rates automatically. Fourth, my results are robust to excluding the Great Recession from the sample period.
This study goes beyond the existing minimum wage empirical literature through the use of highly disaggregated data to study the implications for consumption rather than labor market outcomes, which is arguably a better proxy for well-being. The measurement of the effects of the minimum wage has interested labor economists for decades, with significant contributions made by Neumark and Wascher (1992), Card and Krueger (1994), Lee (1999), and Autor, Manning, and Smith (2016), among others. Yet, only two studies have explored the effect of the minimum wage on consumption. Using the Consumer Expenditure Survey in its Interview version (CEX), Aaronson, Agarwal, and French (2012) measure the expenditure response to minimum wage hikes and find a positive effect, predominantly on vehicle purchases. This effect is very unequally distributed among low-income households, which they interpret as evidence of borrowing constraints and adjustment costs. They also report an insignificant effect of the minimum wage on consumption of a combined category of nondurables and services. However, the measurement of grocery purchases in the CEX may be too noisy to capture this response, and its combination with unresponsive services may further confound the effect.3 Using annual national accounts estimates for metropolitan statistical areas, Cooper, Luengo-Prado, and Parker (2020) find that the minimum wage raises real expenditure in food at home and food away from home. Specifically, they find an elasticity of 0.033 for food at home where I find an elasticity of 0.044 for retail sales. While my estimates are larger, possibly because of my use of finer geographic and time disaggregation, the difference is not statistically significant. Thus, this work complements the existing literature by employing a higher-quality measure of a subset of nondurable expenditure.
The rest of the paper is organized as follows. In Section II, I describe the data and show that retail sales appear to be a reasonable approximation to nondurable consumption aggregates from the national accounts. In Section III, I discuss the identification strategy used to measure the expenditure response to a minimum wage hike. I present the main results in Section IV, and I show robustness checks in Section V. Finally, Section VI concludes.
II. Data Description
My empirical analysis exploits the significant policy heterogeneity across the country and a new measure of consumption by county. In this section, I describe the dispersion in the prevailing minimum wage rates at the county level spanning the period 2006–2014 and show that retail sales data are a good proxy for nondurable consumption.
A. Minimum Wage
The rich variation observed in minimum wage rates emerges from the institutional setting (Figure 1). Federal, state, county, and city governments in the United States can set their own minimum wage. The effective minimum wage rate is the maximum of the four. I disregard changes at the city level when they did not affect the entire county because my controls for local economic conditions are given at the county level.4 The Fair Minimum Wage Act of 2007 increased the federal rate in three steps during my sample period, inducing different changes in the effective rate across states and counties because some had already legislated rates higher than the federal one. Furthermore, 11 states adopted an annual automatic adjustment to their minimum wage rate to compensate for inflation.5 Seventeen other states also legislated higher rates, usually with increments taking place sequentially over a few years. Finally, only six counties had minimum wage rates above the federal or state levels during my sample period.6
The interaction of these county, state, and federal increments produces valuable dispersion in the effective minimum wage rate across the country (Figure 2). For half of the country, predominantly the southern and central regions, the change in the minimum wage between 2006 and 2014 was given by the federal increment (41 percent). For 16 states, the effective minimum wage rose by less than 40 percent in these nine years. Maine had the smallest increment in the period, (that is, only 15 percent). Eight states, mainly in the Mountain division,7 experienced increases above the federal change. As a state, Nevada had the largest increment in the period (that is, 60 percent), but Montgomery County and Prince George’s County in Maryland had even higher increments (that is, 63 percent).
B. Nielsen Sales
To approximate nondurable consumption, I obtain sales by county from a Nielsen data set covering mainly groceries and drugs. The Nielsen Retail Scanner Data contains weekly information on pricing, volume, and merchandising conditions generated by participating retail store point-of-sale systems in all 48 contiguous states and DC, for 2006–2014. It covers approximately 40,000 stores of very diverse sizes (Figure 3).8 The data set contains all the products in Nielsen-tracked categories (that is, food, nonfood grocery items, health and beauty aids, and select general merchandise) that are labeled with a universal product code (UPC). According to Nielsen’s own estimates, the information included represents “more than half the total sales volume of U.S. grocery and drug stores and more than 30 percent of all U.S. mass merchandiser sales volume” (Kilts Center for Marketing 2019).9 Recently, the data set has been used to compute measures of nondurable consumption at geographically disaggregated levels as I do in this study (Kaplan, Mitman, and Violante 2020; Mondragon 2018).10
To distinguish real from nominal effects, I use two measures of sales. Nominal sales aggregate all weekly transactions by store and quarter using current prices. In contrast, real sales aggregate transactions using the 2012 average price for each product across the country. Real sales then remove price changes and price differences across stores, giving a measure of the change in quantities sold. At the store level s, nominal and real sales in quarter t are defined as: where t′ is each week in quarter t, and j is the individual product as defined by its UPC. The price and quantity of product j sold by store s in week t′ are then ps,t′j and qs,t′,j. Finally, is the average price of product j sold across the country in 2012 and is calculated by dividing the total value of sales by the total number of units sold that year.
I collapse sales to the county level, my preferred unit of analysis. I drop all the stores that are not present during the 36 quarters of the sample period. I drop the county of Ringgold in Iowa because it lacks employment data for the fourth quarter of 2013. In total, my sample then includes 2,226 counties across the 48 contiguous states and DC.
Retail sales appear to be a good proxy for nondurable consumption. First, the data provide good geographic coverage, as evidenced by Figure 4, which shows the number of stores in each county. Second, the level and, more importantly, the annual growth rates of retail sales in the period 2006–2014 are consistent with the levels and changes of nondurable consumption estimated by the national accounts at the state level (Figure 5). The correlation between the level of Nielsen sales and nondurable consumption across states is 0.92. In terms of growth rates, the coefficient of regressing the growth rates of nondurable consumption on those of Nielsen sales ranges from 0.65 to 0.80 (Table 1). Given Nielsen sales do not include some nondurable goods, such as gasoline and other fuels, and have low coverage on alcohol, clothing, and appliances, we would not expect a coefficient of one unless all nondurable goods always experienced the same growth rate. Nevertheless, the fact that the estimated coefficient is high suggests Nielsen sales track nondurable consumption reasonably well.
C. Other Sources of Data
Additional variables are used to characterize local economic conditions. I complement the Nielsen and minimum wage data with other publicly available data at the county level: annual population from the Census Bureau’s Population Estimates Program, quarterly data on employment and average weekly earnings from the Quarterly Census of Employment and Wages, house prices from the Federal Housing Finance Agency, and statistics on income distribution from the American Community Survey (ACS). I use nominal gross state product and personal consumer expenditure from the Regional Accounts produced by the Bureau of Economic Analysis. Table 2 displays summary statistics for the resulting county-level data set.
III. Identification Strategy
In this section, I argue a panel data framework is the appropriate choice to study the expenditure response to changes in the minimum wage. Let Salesc,t be the amount of (nominal or real) sales in quarter t in county c located in state s. Then, my baseline model is: where β is the coefficient of interest (that is, the elasticity of sales to the minimum wage). MWc,t is the effective minimum wage rate in county c in quarter t, κc is the county fixed effect, τt is the time fixed effect, and Xc,t is a set of observables at the county or state level (in my preferred specification: employment, population, gross state product, and house prices).11 The first-difference operator is denoted by Δ, such that Δlog(Salesc,t) = log(Salesc,t) − log(Salesc,t–1).
My identification strategy rests on the assumption of conditional parallel trends across counties. I assume that conditional differences between those counties where the minimum wage increased and those where it did not would have remained constant in the absence of a minimum wage hike. This assumption does not require that every county would have grown at the same pace during the sample period; rather, it requires that the mean growth in sales that cannot be explained by growth in local economic conditions and unobservable constant characteristics would have been the same across counties if the minimum wage increments had not taken place.
The use of panel data is important to control for fixed unobservable heterogeneity in growth rates. Counties where the minimum wage is high could be counties where the average wage is also high, so a cross-sectional estimate would not yield the impact of the policy, but, instead, would simply reflect that richer counties consume more. Furthermore, counties with high minimum wages could experience, on average, higher or lower sales growth rates reflecting features of their structural transformation or industrial relations. County fixed effects solve this challenge by capturing all the static county characteristics affecting the growth rate in sales. The specification in first differences then allows for each county to have its own average growth rate in sales over the period. This is a weaker identification assumption than the one imposed by the specification in levels usually found in the literature (for example, Dube, Lester, and Reich 2010; Neumark, Salas, and Wascher 2014b).12
My econometric model allows for a flexible specification of time trends. Time fixed effects capture any shocks affecting all counties equally, including seasonality. Additionally, in my preferred specification I control for local observable economic conditions, allowing different counties to experience different unconditional trends. The inclusion of such controls is important in the context of the Great Recession, which hit different regions with different degrees of severity and where the magnitude of those effects could potentially be correlated with the changes in the minimum wage. Failing to control for local conditions would bias the estimates. However, the inclusion of these controls comes at the cost of some endogeneity concerns because sales, employment, and house prices could be jointly determined. For this reason, I present results both with and without local controls. In general, I find that the estimates for the elasticity of sales to the minimum wage are stable across specifications, attenuating concerns on misspecification.
Because my goal is to obtain a measure of the aggregate response of retail sales to the minimum wage, I weight counties using their population level in the 2010 census. Given Nielsen tracks more stores in more heavily populated areas, this approach also gives more weight to the counties where sales are better measured. I cluster standard errors at the state level to account for any possible serial correlation and for the bias introduced by the minimum wage policy being the same (usually) for all the counties within the state (Bertrand, Duflo, and Mullainathan 2004).
IV. Results
A. Baseline Results
Nominal sales increase by 0.6 percent after a 10 percent minimum wage hike, a response that is both economically and statistically significant (Table 3). Specifications 1–4 are increasingly rich in their controls for local economic conditions, ranging from no controls to controlling for employment, population, gross state product, house prices, and earnings. Specification 5 includes a Bartik-style employment shock combining national-level industry growth and initial industry composition at the county level in 2005.13 Specification 6 complements all existing controls for local economic conditions in Specification 4 with the Bartik shock of Specification 5. Specification 7 drops county fixed effects from Specification 6. My preferred specification, Specification 3, balances appropriate controls and endogeneity concerns and yields the most conservative estimate of the elasticity of nominal sales to the minimum wage: 0.063. However, the point estimate is fairly stable across specifications, oscillating between 0.063 and 0.068. While the addition of controls does not change the point estimates significantly, it does improve their precision.
The estimated response of nominal sales is in line with recent estimates in the literature. Using personal consumer expenditure at the level of metropolitan statistical area, Cooper, Luengo-Prado, and Parker (2020) find that a 10 percent increase in the minimum wage raises nominal consumption of food at home by 0.3 percent and food away from home by 0.9 percent within a year. Their specification is akin to Specification 5 in Table 3 where they control for exogenous employment shocks through a Bartik instrument. Instead, I prefer to control directly for local economic conditions to incorporate the heterogeneous dynamics that counties experienced in the lead up to and the aftermath of the Great Recession. The stability of the results across specifications suggests the choice of controls may not matter much. Additionally, my specifications are estimated at the quarterly level and do not require averaging minimum wage rates across different jurisdictions, which could explain my slightly higher estimates. Moreover, my data set covers only a subset of consumption goods, while theirs is broader.
Real sales also rise significantly after a minimum wage increment. The point estimate for the elasticity ranges from 0.044 in my preferred specification to 0.048, and it is statistically significant at the 10 percent level in five of the seven specifications. In each specification, the real sales elasticity is around 0.02 points lower than the nominal sales elasticity.14
Even if the difference between the nominal and real sales elasticities is not statistically significant, it suggests some of the increase in sales emerges from consumers paying higher prices. It could be that stores raise prices in response to higher demand and higher costs, or consumers change their shopping behavior after an increase in the minimum wage, replacing cheap stores with expensive ones and therefore increasing nominal expenditures more than real quantities.15 Prices rising by 0.2 percent after a minimum wage increase of 10 percent is within the range of recent estimates. Using store-level data, after a 10 percent minimum wage increase, Montialoux, Renkin, and Siegenthaler (2017) find higher prices by 0.3–0.5 percent, while the response is between 0.6 and 0.8 percent in Leung (2021) and not statistically significant in Ganapati and Weaver (2017). Using input–output tables, MaCurdy (2015) finds that prices of groceries would rise by 0.2 percent assuming full pass-through of higher labor costs and equal minimum wage increases across all states along the supply chain.16 ,Cooper, Luengo-Prado, and Parker (2020) find that a 10 percent increase in the minimum wage increases the local consumer price index (CPI) by 0.1 percent, but the response is largely driven by food away from home, whereas their estimation of the response of prices for food at home is not statistically significant.17
While the estimated elasticity is large, it appears plausible (Table 4). If the minimum wage at the end of 2014 had been raised to $10.10, it would have implied an average increase of 28.2 percent across the country.18 Given that Nielsen sales amounted to $187 billion in 2014, the minimum wage hike would have produced additional nominal sales of $3.3 billion per year, a tenth of the increase in labor income for low-wage workers estimated by Congressional Budget Office (2014).19 Assuming all nondurable goods were to react by the same magnitude, nominal nondurable consumption would rise by $48 billion. A third of the increase in nondurable consumption (that is, $14 billion) could be attributed to higher prices and, therefore, would likely be borne disproportionately by relatively richer households, who consume more.20 The remaining two-thirds of the increase in nondurable consumption, (that is, $33 billion) would correspond to higher quantities. The increase is slightly higher than the $32 billion of higher labor income predicted by Congressional Budget Office (2014), but the 95 percent confidence interval extends from -$5 billion to $71 billion.21
The results suggest a high marginal propensity to spend on nondurables out of minimum wage hikes among low-wage workers, which may not be unreasonable. First, minimum wage hikes are permanent nominal income shocks, so standard life-cycle consumption theory would predict high marginal propensities to spend out of them absent high levels of inflation.22 Second, most minimum wage workers live in low-income households and, therefore, are more likely to be financially constrained and to exhibit a high marginal propensity to spend. Even the minimum wage workers who live in high-income households could have high marginal propensities to spend if they make their own consumption decisions, as implied in the hypothesis of the “hungry teenagers.”23 Third, given that a minimum wage hike is a permanent shock to income, borrowing constraints may loosen (Aaronson, Agarwal, and French 2012; Cooper, Luengo-Prado, and Parker 2020; Dettling and Hsu 2017). Fourth, under homothetic preferences, lack of adjustment costs, and perfect divisibility of goods, consumption of different goods would be expected to rise at the same rate. Yet, Cooper, Luengo-Prado, and Parker (2020) fail to find a significant increase in real expenditure on durable goods and services other than food away from home, and Aaronson, Agarwal, and French (2012) find an increase in purchases of durable goods only for a small group of households. Thus, the existing evidence suggests low-wage workers may be spending a substantial share of their higher labor income on nondurable goods.
B. Sales Elasticity by Fraction of Workers Affected by the Minimum Wage
Next, I exploit cross-county heterogeneity by interacting the (log) minimum wage with the fraction of households making less than $15,000 a year, who are more likely to earn the minimum wage.24 More precisely, I estimate the regression: where Fractionc is the fraction of households making less than $15,000 a year. In this context, the elasticity of sales to the minimum wage in county c is given by β1 + β2 Fractionc.
Low-income households are more likely to earn minimum wages. From the Current Population Survey in 2014, 26.9 percent of households with an annual income below $15,000 had at least one member earning the minimum wage, but the share was only 7.9 percent for households with an annual income above $15,000. Therefore, households with an annual income below $15,000 are 3.4 times more likely to have at least one member earning the minimum wage than richer households.25 At the state level, the correlation between the fraction of households making less than $15,000 a year and the fraction of workers earning the minimum wage is 0.6 and highly statistically significant.26
Counties with more low-income households exhibit a greater elasticity of sales to the minimum wage (Table 5). I report the sales elasticities evaluated at two different in-sample levels of the fraction of households making less than $15,000 a year: 36.1 percent and 5.0 percent, which correspond to the 99th and first percentiles of the distribution, respectively. In counties where more than a third of the households report a low income, nominal sales rise by more than 1.2 percent in response to a 10 percent minimum wage hike, and the estimate is statistically significant at the 5 percent level. In such counties, real sales increase by 0.95 percent, with statistical significance at 10 percent. On the other hand, when only 5 percent of the households report a low income in the county, the estimated elasticity is basically zero and not statistically significant both for nominal and real sales. However, the difference is not statistically significant.
C. Sales Elasticity Exploiting Within-State Variation
Here I further refine the identification strategy by interacting the minimum wage with a measure of the bindingness of the policy and incorporating state-by-period fixed effects. Formally, I estimate the following regression: where τs,t represents state-by-period fixed effects. I explore three different measures of bindingness: the share of households in the county with an annual income lower than $10,000, $15,000, and $25,000. This exploits the fact that counties with larger fractions of low-income households are more likely to be affected by the policy.
This approach strengthens the credibility of my identification strategy by focusing exclusively on within-state variation. While my data include a few counties that have established their own minimum wage rates above the state level, the vast majority of the variation exploited in this study comes at the state level. By interacting the minimum wage with the fraction of low-income households, β measures the differential impact of the minimum wage in counties where the policy binds more tightly by comparing them with other counties within the same state but where the policy binds less tightly. State-by-period fixed effects then capture any observable and unobservable dynamics at the state level and allow for a stronger identification case. To the extent that minimum wage changes are uncorrelated with unobservable county-specific time trends, the estimates of the differential response across counties are causal. For example, a concern of reverse causality for my baseline specification could emerge if states raised their minimum wage rates in response to state economic conditions not accounted for by the controls. By including state-by-period fixed effects such concern would be addressed as long as changes in the minimum wage were driven by state-level conditions and not by the conditions in particular counties.
I find that the expenditure response is indeed stronger in counties where the minimum wage binds more tightly, even after allowing for state-specific unobservable and heterogeneous time trends, despite the strong requirements on the data imposed by this identification strategy (Table 6). Using the fraction of households with income below $10,000, the differential elasticity is 0.969 for nominal sales and 0.886 for real sales, both of which are statistically significant at the 5 percent level. For interpretation, consider the case of Texas, where Willacy County had the highest share of households with income below $10,000 in the country in 2005 (that is, 29.8 percent). Within Texas, Rockwall County had the lowest share of households with income below $10,000 (that is, 2.7 percent). Therefore, after a 10 percent increase in the minimum wage in Texas, growth in nominal sales would have been 2.6 percentage points higher in Willacy than in Rockwall, while real sales growth would have been 2.4 percentage points higher.27 This result is robust to using other income thresholds, such as $15,000 and $25,000, with point estimates becoming smaller as the income threshold expands. All estimates for nominal sales are statistically significant at the 5 percent level. The estimate for real sales with a $15,000 threshold is statistically significant at the 10 percent level and at the 11 percent with a $25,000 threshold.
V. Robustness
In this section, I show that the dynamic response to the minimum wage is concentrated in the first quarter after the new rate is enacted and that my results are robust to spatial unobservable heterogeneity in time trends, as well as to excluding the Great Recession and indexing states.
A. Dynamic Response to the Minimum Wage
I explore the dynamic response to the minimum wage by estimating a dynamic version of my preferred specification with five leads and three lags, spanning two years:
I convert the λj estimates into event study effects (Schmidheiny and Siegloch 2019): where coefficient βj can be interpreted as the change in sales accumulated j quarters after the minimum wage rose, for nonnegative values of j. For negative values of j, βj, captures the accumulated response prior to the minimum wage change, with j=–1 normalized to zero.
The impact of the minimum wage is concentrated in the first quarter after the policy is implemented (Figure 6). Nominal sales grow by 0.5 percent immediately after a minimum wage hike of 10 percent, an estimate that is statistically significant at the 1 percent level. The response remains positive for the two following quarters, but without accelerating significantly. Similarly, real sales exhibit a statistically significant response at the 6 percent level in the first quarter, with sales growing by 0.3 percent. Over time, the effect dissipates, and by the end of the third quarter, the cumulative response is not statistically significant.
Some evidence of pretrends in sales could point to anticipation effects or inappropriate estimation by the distributed-lag design. A joint F-test for the leads rejects that all coefficients are zero with a confidence of 84 percent for nominal sales and 93 percent for real sales. Both for nominal and real sales, the cumulative anticipated response to the minimum wage is only statistically significant at the 5 percent level three quarters before the minimum wage change. This negative pretrend could be explained by anticipation to the policy. While we would not expect minimum wage workers to raise their spending before they get a raise if they are financially constrained, stores could raise prices in anticipation of higher future costs, or disemployment effects could materialize before the policy is enacted. However, the magnitude appears too high for it to be solely anticipation effects. On the other hand, rather than anticipation, the three-quarters-ahead lead in the specification could be picking up the effect of the previous-year minimum wage hike, given that increases took place on a regular, annual basis for many states in my sample. A high degree of collinearity in minimum wage changes could lead to a weak estimation of the coefficients of interest and could explain the wide confidence intervals.28 Finally, heterogeneity in treatment, as shown in Sections IV.B and IV.C, together with nonsimultaneous enactment, could yield contaminated estimates of leads and lags (Sun and Abraham 2020; Callaway and Sant’Anna 2018). Thus, these results do not necessarily reject my identification assumption.
B. Robustness to Unobservable Spatial Heterogeneity in Time Trends
I provide further evidence that my results are robust to the presence of unobservable spatial heterogeneity in time trends by allowing more geographically granular time fixed effects.29 My baseline estimates are from a specification in first differences with county fixed effects; therefore, they already allow for a heterogeneous average growth rate in sales at the county level. In addition, Section IV showed the minimum wage had a differential impact on counties with high shares of low-income households after allowing for state-by-period fixed effects. Nevertheless, I further test the robustness of my estimates by exploiting only the variation within regions and divisions.
My baseline estimates remain stable and statistically significant after allowing for census region-by-period and division-by-period fixed effects and state-specific linear trends (Table 7). The point estimates range from 0.055 to 0.071 for nominal sales and from 0.050 to 0.061 for real sales. The standard errors are larger than in the baseline, reflecting the reduced variation exploited by the identification approach, but all coefficients are still significant at the 10 percent level.
C. Other Robustness Checks
In this section, I show that my results are robust to excluding states that index their minimum wage rates and to excluding the Great Recession.
The expenditure response to the minimum wage does not vary significantly after excluding indexing states (Specification 1 in Table 8). As discussed in Section II, 11 states indexed the minimum wage to the cost of living at some point during my sample period. For ten of these 11 states the adjustment follows the federal inflation rate, so it is more likely to be exogenous to local economic conditions. However, if this automatic adjustment of the minimum wage rate induces structural changes in the state economy that make it more responsive to the policy (for example, it could be that, as a consequence of the indexing, the federal inflation rate becomes more widely used for wage negotiation in the state, so federal inflation leads to a higher minimum wage rate in the state but also to higher wages in general), my estimate would overstate the effect of a minimum wage increment. The bias could be in the opposite direction as well; Brummund and Strain (2020) find evidence of larger disemployment effects in indexing states. To explore this concern, I drop indexing states from the sample. A 10 percent minimum wage hike increases nominal sales by 0.55 percent in the nonindexing states, only slightly less than the 0.63 percent estimated in my preferred specification. Real sales also have a point estimate slightly lower for nonindexing states. The nominal sales elasticity after restricting the sample to nonindexing states is statistically significant at the 5.5 percent level and at the 16.3 percent level for real sales.
My results are also robust to excluding the Great Recession from the sample period (Specification 2 in Table 8). If the severity of the recession that followed the bust of the housing bubble was correlated with changes to the minimum wage beyond what is captured by controlling for house prices and other local economic variables, my identification strategy could yield biased estimates. To explore this possibility, I drop from the sample observations between the fourth quarter of 2007 and the second quarter of 2009 (that is, the span of the Great Recession according to the NBER). I find that both the nominal and real sales elasticities remain largely unchanged and statistically significant at the 5 percent level.
VI. Conclusions
I exploited variation in minimum wage rates within the United States and a novel data set on retail sales by county to show that the minimum wage raises aggregate nondurable consumption. I find that a 10 percent increment in the minimum wage increases nominal sales by 0.6 percent and real sales by 0.4 percent. Consistent with economic theory, the expenditure response is found to be larger in counties where the minimum wage binds more. By leveraging heterogeneity in bindingness across counties, I further show that the impact of minimum wage hikes is positive and significant even when exploiting only within-state variation.
My results confirm that the minimum wage is an effective policy to increase aggregate demand modestly and are suggestive of high marginal propensities to spend on nondurables among low-wage workers. Further research will be necessary to expand our understanding of the implications of the minimum wage for well-being by looking at both the intended and unintended effects on other outcomes, such as inequality, capital accumulation, and economic growth.
Footnotes
The author thanks Greg Kaplan for valuable advice at each stage of this project. He is also grateful for comments from Mark Aguiar, Will Dobbie, Alexander Jakobsen, Seth Kerstein, Alan Krueger, Alexandre Mas, Alexander Massara, Atif Mian, Benjamin Moll, Ezra Oberfield, Michael Reich, Richard Rogerson, Mark Watson, Justin Weidner, Juan Pablo Xandri, three anonymous referees, and participants at the Macro Student Workshop at Princeton University and at the 2016 Royal Economic Society Symposium of Junior Researchers at the University of Sussex. The author declares that he has no relevant or material financial interests that relate to the research described in this paper. The conclusions drawn from the Nielsen data are those of the researcher(s) and do not reflect the views of Nielsen. Nielsen is not responsible for, had no role in, and was not involved in analyzing and preparing the results reported herein. Alonso’s own analyses are calculated (or derived) based in part on data from The Nielsen Company (US), LLC and marketing databases provided through the Nielsen Datasets at the Kilts Center for Marketing Data Center at The University of Chicago Booth School of Business. The data can be obtained by filing a request directly with the Data Center at The University of Chicago Booth School of Business (https://www.chicagobooth.edu/research/kilts/datasets/nielsen). Additionally, the other data sets, which are compiled from publicly available data, and all accompanying statistical programs can be obtained from the author from November 2020 and through May 2022 (cristianalonso86{at}gmail.com).
↵1. These calculations take into account that some counties and states had already set rates above the federal level of $7.25.
↵2. Minimum wage workers could be financially constrained if they belong to low-income households, but also if they belong to richer households and make their own consumption decisions.
↵3. In the CEX, households are asked the usual amount of weekly expense for grocery shopping and not the actual amount spent in a given and recent week, where recall could be higher.
↵4. Federal and state-level minimum wage rates were retrieved from the federal and state Departments of Labor. County-level minimum wages were obtained from Vaghul and Zipperer (2016). According to Vaghul and Zipperer (2016), 27 cities and unincorporated areas enacted their own legislation during my sample period. An alternative to disregarding these changes would have been to obtain county-level minimum wages by weighting the city-level minimum wage rates by population. I choose not to do so because at such a fine level of geographic disaggregation, it is harder to argue the minimum wage rate would only apply to the city population. Results are robust to excluding these counties.
↵5. These states and years the automatic adjustment was approved are Arizona (2006), Colorado (2006), Florida (2004), Missouri (2006), Montana (2007), Nevada (2006), New Jersey (2013), Ohio (2006), Oregon (2002), Vermont (2005), and Washington (1998).
↵6. Counties that enacted their own minimum wage legislation during my sample period are San Francisco, CA; Johnson County, IA; Lexington, KY; Louisville, KY; Montgomery County, MD; and Prince George’s County, MD.
↵7. Mountain division as defined by the U.S. Census Bureau, which includes Arizona, Colorado, Idaho, New Mexico, Montana, Utah, Nevada, and Wyoming.
↵8. For comparison, according to the 2012 Statistics of U.S. Businesses, there were 145,624 food and beverage stores, 92,423 health and personal care stores, and 48,872 general merchandise stores.
↵9. Mass merchandisers are retailers who sell groceries and multiple other items, such as appliances, accessories, clothing, furniture, etc.
↵10. Recent work has also used this data set to compute price indexes at geographically disaggregated levels (for example, Beraja, Hurst, and Ospina 2019;Leung 2021). Furthermore, Ehrlich et al. (2019a,b) argue for improving national account statistics by leveraging this kind of data set.
↵11. I use nominal gross state product to account for both state-level inflation and economic growth.
↵12. A previous version of this study estimated the equation in levels instead of first differences. The elasticities found with the specifications in levels tend to be larger and statistically significant, but more dependent on the specific set of controls included. Results available upon request. Cooper, Luengo-Prado, and Parker (2020) also use first differences.
↵13. Industry is defined at the two-digit level and includes public and private employment.
↵14. Nielsen data also allow me to estimate expenditure responses for particular product groups. Point estimates tend to be higher for General Merchandise (0.102 for nominal sales and 0.095 for real sales) than for Health and Beauty Aids (0.052 and 0.029) and Food (0.066 for nominal sales), with statistical significance at levels ranging from 5 to 12 percent. Expenditure responses for Non-Food Groceries and Alcohol are not statistically significant. Results available upon request.
↵15. For comparison, costs for grocery stores could rise by 0.05 percent after a minimum wage hike of 10 percent due to a higher wage bill. Reich et al. (2016) calculate that labor costs represent 12.2 percent of operating costs for grocery stores. Using the CPS in 2014, I estimate that 13.4 percent of the retail workers would be directly affected by a 10 percent increment in the minimum wage. If the amount of labor hired did not change, and there were no spillovers beyond the new minimum wage level, the wage bill would rise by 0.4 percent, leading to higher total costs by 0.05 percent. Full pass-through of these higher costs would explain a quarter of the difference between the nominal and real responses.
↵16. MaCurdy (2015, Table 3) shows that the price of “food: inside home” grew by 0.34 percent after a 21.2 percent increment in the minimum wage.
↵17. A significant response of prices of food away from home is also found by Aaronson, French, and MacDonald (2008).
↵18. The federal minimum wage in 2014 was $7.25, but given that many states and counties had higher rates, the effective population-weighted minimum wage rate was $7.88.
↵19. I use the elasticity of nominal sales estimated in Specification 3 of Table 3. While that elasticity is for the quarter during which the policy is implemented, I show in Section V that the response to the minimum wage is indeed concentrated in the first quarter.
↵20. The impact of higher prices is estimated from the difference between the elasticities of nominal and real sales in Specification 3 of Table 3.
↵21. These estimates could overstate the impact of the minimum wage on nondurable consumption for at least two reasons. First, the responsiveness of other categories of nondurables to the minimum wage may be lower than that of retail sales. For example, in their meta-analysis, Havranek and Kokes (2015) find a mean short-term income elasticity of gasoline demand of only 0.28, and Nelson (2013) finds a mean income elasticity of 0.60 for total alcohol. Second, to the extent that the minimum wage works by redistributing income from capital-owners to low-wage workers, by identifying the impact at the local level, my estimates would not capture the negative expenditure response of households negatively affected by the minimum wage hike if they live in a different area. On the other hand, food away from home could also rise after a minimum wage hike. Cooper, Luengo-Prado, and Parker (2020) find an elasticity of 0.052 for real consumption of this service, which would add another $9.5 billion of real spending in 2014 dollars after raising the minimum wage to $10.10.
↵22. For example, Reich et al. (2016) estimate the aggregate demand effects of the New York proposed minimum wage increments with marginal propensities to consume that exceed one for households with less than $75,000 of income. Edwards (2004) estimates a high marginal propensity to spend out of Earned Income Tax Credit checks. Also, note that minimum wage hikes are almost never reversed. There has only been one case in which minimum wages hikes were reverted recently, and it happened after my sample period. The Kentucky Supreme Court declared illegal minimum wage ordinances by Lexington and Louisville counties in late 2016. Certainly, the permanent income shock would be less so if the likelihood of being unemployed rose sharply, but that is far from settled in the literature. Since the influential work by Card and Krueger (1994), small or insignificant employment elasticities have usually been found for restaurant workers (Dube, Lester, and Reich 2010; Allegretto et al. 2017; Neumark, Salas, and Wascher 2014b; Addison, Blackburn, and Cotti 2015). Jardim et al. (2017) do find a large disemployment effect among low-wage workers, while Meer and West (2016) argue that large disemployment effects may emerge over time by lowering the growth rate of employment. For teens, Neumark, Salas, and Wascher (2014a) find an elasticity close to −0.15, whereas Allegretto, Dube, and Reich (2011) argue that negative elasticities are only the result of heterogeneous unobservable time trends unrelated to the minimum wage. Using data from the wage distribution, while Cengiz et al. (2019) do not find a disemployment effect, Clemens and Wither (2019) do.
↵23. Congressional Budget Office (2014) estimates that less than a third of the minimum wage workers live in households with income above three times the poverty line. Kennan (1995) proposed the hypothesis of “hungry teenagers” as an explanation for the lack of disemployment effects in the restaurant industry after minimum wage hikes. It suggests that low-wage workers may spend their higher labor income on low-wage products. Aaronson, French, and MacDonald (2008) find evidence along this line.
↵24. The ACS reports the fraction of households with total income lower than certain thresholds by county, providing a rough measure of income distribution at the local level. In 2014, a full-time worker making the minimum wage earned between $15,080 ($7.25, federal rate) and $19,760 ($9.50, rate in DC).
↵25. More broadly, Congressional Budget Office (2014) estimates that households living on incomes under the poverty threshold in the second half of 2016 (that is, $18,700 for a family of three and $24,100 for a family of four) are overrepresented as low-wage workers (that is, people paid less than $11.5 per hour). While they account for 6 percent of all workers, they represent 20 percent of all low-wage workers. In fact, 50 percent of low-wage workers belong to households living on less than twice the poverty threshold.
↵26. Unfortunately, it is not possible to identify the share of minimum wage workers at the county level because worker-level surveys do not include county identifiers in their publicly available versions.
↵27. 2.6% = (0.298 – 0.027) × 0.969 × 10% and 2.4% = (0.298 – 0.027) × 0.886 × 10%.
↵28. Interestingly, there is no evidence of pretrends when the estimation is in levels.
↵29. The desirability of local area controls to account for unobservable and heterogeneous time trends is at the center of an ongoing debate in the literature measuring the impact of the minimum wage on labor market outcomes (Dube, Lester, and Reich 2010; Allegretto et al. 2017; Neumark, Salas, and Wascher 2014a,b).
- Received May 2018.
- Accepted May 2020.
References
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