WHAT EXPLAINS TEMPORAL AND GEOGRAPHIC VARIATION IN THE EARLY US CORONAVIRUS PANDEMIC? Hunt Allcott Billy A. Ferguson New York University & NBER Stanford University Levi Boxell Matthew Gentzkow Stanford University Stanford University & NBER Jacob C. Conway Benny Goldman Stanford University Harvard University October, 2020 Working Paper No. 20-040 NBER WORKING PAPER SERIES WHAT EXPLAINS TEMPORAL AND GEOGRAPHIC VARIATION IN THE EARLY US CORONAVIRUS PANDEMIC? Hunt Allcott Levi Boxell Jacob C. Conway Billy A. Ferguson Matthew Gentzkow Benny Goldman Working Paper 27965 http://www.nber.org/papers/w27965 NATIONAL BUREAU OF ECONOMIC RESEARCH 1050 Massachusetts Avenue Cambridge, MA 02138 October 2020 We thank Zane Kashner for his research assistance. We thank SafeGraph, Facteus, and Homebase for providing access to the data. We also thank the SafeGraph and Homebase COVID-19 response communities respectively for helpful input. We also thank seminar participants at Harvard University and Stanford University for their feedback and comments. We acknowledge funding from the Stanford Institute for Economic Policy Research (SIEPR), the John S. and James L. Knight Foundation, the Sloan Foundation, the Institute for Humane Studies, and the National Science Foundation (grant number: DGE 1656518). Previously circulated beginning in May 2020 as “Economic and Health Impacts of Social Distancing Policies during the Coronavirus Pandemic.” The views expressed herein are those of the authors and do not necessarily reflect the views of the National Bureau of Economic Research. At least one co-author has disclosed a financial relationship of potential relevance for this research. Further information is available online at http://www.nber.org/papers/w27965.ack NBER working papers are circulated for discussion and comment purposes. They have not been peer-reviewed or been subject to the review by the NBER Board of Directors that accompanies official NBER publications. © 2020 by Hunt Allcott, Levi Boxell, Jacob C. Conway, Billy A. Ferguson, Matthew Gentzkow, and Benny Goldman. All rights reserved. Short sections of text, not to exceed two paragraphs, may be quoted without explicit permission provided that full credit, including © notice, is given to the source. What Explains Temporal and Geographic Variation in the Early US Coronavirus Pandemic? Hunt Allcott, Levi Boxell, Jacob C. Conway, Billy A. Ferguson, Matthew Gentzkow, and Benny Goldman NBER Working Paper No. 27965 October 2020 JEL No. H7,H79,I1,I12 ABSTRACT We provide new evidence on the drivers of the early US coronavirus pandemic. We combine an epidemiological model of disease transmission with quasi-random variation arising from the timing of stay-at-home orders to estimate the causal roles of policy interventions and voluntary social distancing. We then relate the residual variation in disease transmission rates to observable features of cities. We estimate significant impacts of policy and social distancing responses, but we show that the magnitude of policy effects is modest, and most social distancing is driven by voluntary responses. Moreover, we show that neither policy nor rates of voluntary social distancing explain a meaningful share of geographic variation. The most important predictors of which cities were hardest hit by the pandemic are exogenous characteristics such as population and density. Hunt Allcott Billy A. Ferguson Department of Economics Graduate School of Business New York University Stanford University 19 W. 4th Street, 6th Floor 655 Knight Way New York, NY 10012 Stanford, CA 94305 and NBER billyf@stanford.edu allcott@post.harvard.edu Matthew Gentzkow Levi Boxell Department of Economics Stanford University, Stanford University Department of Economics 579 Jane Stanford Way 579 Jane Stanford Way Stanford, CA 94305 Stanford, CA 94305 and NBER Lboxell@stanford.edu gentzkow@stanford.edu Jacob C. Conway Benny Goldman Stanford University Harvard University Department of Economics bgoldman@g.harvard.edu 579 Jane Stanford Way Stanford, CA 94305 jcconway@stanford.edu 1 Introduction The course of the novel coronavirus pandemic in the US has varied dramatically across space and time. In the early months, the epicenter was primarily large cities on the west coast and in the northeast. Slow growing outbreaks in Seattle and San Francisco were followed by rapid surges of cases in cities such as New York and Boston. Other large cities such as Dallas, Atlanta, Phoenix, Miami, and Denver were largely spared. Popular discussion and prior work have pointed to a number of plausible drivers of this vari- ation, with policy differences as one leading explanation.1 However, evidence below and in prior work shows clearly that substantial behavioral changes preceded the first stay-at-home orders, and that mobility levels have remained significantly depressed even after many of these policies were lifted—suggesting voluntary social distancing behaviors may be important. Other potential drivers include physical characteristics of cities such as population size and density that could be expected to affect virus transmission rates, or connections via international flights to early overseas epicen- ters such as China and Italy. Clear empirical evidence on the roles of these factors is essential to understanding the course of the epidemic to date and steering policy responses going forward. In this paper, we provide new evidence on the importance of policy relative to these factors in the first months of the US pandemic. Our empirical strategy exploits short-run changes around the onset of policy in event-study and difference-in-difference specifications within the context of an SIRD (Susceptible, Infected, Recovered, Deceased) model of disease transmission. By taking the ratio between the estimated effects of policy on disease transmission and the estimated effects of policy on social distancing behaviors, we are able provide causal estimates for the change in disease transmission rates per unit change in social distancing—allowing us to decompose the role of policy and social distancing behaviors in driving the temporal and geographic variation in the pandemic. We then relate the residual variation in disease transmission rates to observable features of cities. We begin by using event-study designs to estimate the short-run effects of stay-at-home orders on social distancing. We measure social distancing using visits to points of interest (POIs) such as shops, parks, hospitals, and other places measured in cell phone location data aggregated by a company called SafeGraph. We combine POI visits with data on the implementation date of stay- 1 Forexample, New York Governor Andrew Cuomo has frequently been blamed for the severity of the crisis in New York, with critics citing his slow response to the pandemic and his derision of Mayor De Blasio’s earlier suggestion of closing down New York City (Gold and Robinson 2020). 2 at-home orders and collapse by combined statistical area (CSA). Our estimates suggest that POI visits drop by 18 percent on the day after a stay-at-home order is implemented. We complement our GPS data with information on consumer spending and small business employment—finding that consumer spending drops by 7 percent and employment drops by 12 percent. We next estimate the effects of stay-at-home orders on disease transmission in the context of an SIRD epidemiological model (Kermack and McKendrick 1927). Infected people infect Susceptible people at rate βt and recover at rate γ. The reproduction number R—the number of people to whom one Infected person transmits the virus—is βt /γ. If a stay-at-home order is modeled as a proportional effect τ on the contact rate, then we can estimate τ in a linear regression framework with the natural log of the number of new cases on the left-hand side. We find that stay-at-home orders reduce the contact rate by 9–14 percent for different plausible values of γ. Using simulation models, we show that non-model-based regression frameworks used in some other recent papers to estimate the effects of stay-at-home orders can produce biased results. We use these estimates to examine the share of the temporal variation in health, social distanc- ing, and economic outcomes that can be attributed to stay-at-home orders versus voluntary and other policy responses. Consistent with other work released around the same time as our initial May 2020 working paper, we find that much of the reduction in POI visits pre-dates stay-at-home orders (Brzezinski et al. 2020; Chetty et al. 2020; Gupta et al. 2020; Villas-Boas et al. 2020). We calculate that by mid-April 2020, the short run effects of stay-at-home orders accounted for only 16 percent of observed social distancing, 16 percent of observed reductions in economic activity (measured by small business employment), and 13 percent of the reduction in contact rate. Next, we use our previous estimates to compute the counterfactual transmission rates if policy, and subsequently social distancing rates, were equalized across all CSAs. We find that neither policy nor social distancing rates explain the geographic variation in transmission rates. Rather, fixed differences across CSAs are the primary drivers. Using a Lasso model to select features of the data that are highly predictive of differential transmission rates, we find that population and population density explain nearly half of the average differences across high and low transmission CSAs, with racial composition and partisanship explaining a smaller share. Our model accurately predicts transmission rates in epicenters, such as New York City. These results suggest that much of the observed variation across CSAs was not driven by different policy or voluntary behavioral responses, but was driven by invariant characteristics of CSAs. Lastly, we use our estimates to examine the effect of counterfactual policies on the overall 3 prevalence of the virus in the United States. While policy explains a small proportion of the temporal variation in case growth and an even smaller proportion of the geographic variation, policy still has led to an important reduction in cases. Absent the observed policy response, there would have been 494,000 more confirmed cases by April 30th and 14,800 more deaths. Moreover, a uniform stay-at-home order implemented on March 17 would have resulted in 154,000 fewer cases by April 30th. We emphasize a number of important caveats. Our GPS-based social distancing measure cap- tures overall movement patterns without distinguishing activity with a high vs. low risk of virus transmission. Our measures of economic cost only capture two dimensions of policies’ overall economic impact, and these only imperfectly. Our measure of health impact relies on the assump- tions of our SIRD model, is overall relatively imprecise, and may be biased by factors such as endogenous reporting of coronavirus cases. In each case, we are able to capture only short-term, on-impact effects. We provide a set of data points that speak to the benefits and costs of social distancing policies but stop well short of a comprehensive welfare analysis. Moreover, our analy- sis focuses on the early onset of the pandemic. Predictors and drivers of temporal or geographic variation later in the pandemic may be different. Our work connects to several active research areas. First, a series of recent papers uses GPS data from SafeGraph or similar providers to quantify social distancing and estimate the effects of stay-at-home orders and other policies (Alexander and Karger 2020; Allcott et al. 2020; Chen et al. 2020a; Engle et al. 2020; Goolsbee and Syverson 2020; Painter and Qui 2020; Villas-Boas et al. 2020). Second, several recent papers have studied the effects of stay-at-home policies on economic outcomes (Baker et al. 2020; Bartik et al. 2020; Chen et al. 2020b; Chetty et al. 2020; Kong and Prinz 2020). Third, another set of papers quantifies the effects of regulation on health outcomes (Childs et al. 2020; Flaxman et al. 2020; Fowler et al. 2020; Friedson et al. 2020; Greenstone and Nigam 2020; Lasry et al. 2020). In the epidemiological literature, there are a set of what economists might call “structural” models that use Bayesian techniques to estimate the reproduction number R; these estimates often pay less attention to identifying the causal effect of policies on R (Cori et al. 2013; Thompson et al. 2013). In the economics literature, there are a set of papers that use reduced form event study approaches to estimate the effects of policies on some measure of disease transmission, but many of these papers are not closely tied to structural models. Our paper forms a bridge between these two lines of work by deriving simple linear estimating equations (which are useful for standard quasi-experimental analysis) from structural 4 epidemiological models and using these estimates to decompose the role of various drivers in explaining the temporal and geographic variation of virus transmission in the early months of the pandemic.2 Section 2 describes the data. We present estimated effects of stay-at-home policies on social distancing and economic outcomes in Section 3 and on health outcomes in Section 4. Section 5 analyzes the variation in COVID-19 outcomes across time within a geography as well as across geographies. 2 Data 2.1 Policy Data We explore both stay-at-home and business closure policies in this paper. Due to the decentral- ized policy response of states, cities, and counties, there is no single resource documenting non- pharmaceutical interventions (NPIs) in the United States. To get the best coverage of these NPIs, we combine data from four sources and define both our stay-at-home and business closure policies by sequentially assigning enforcement dates by data source. We prioritize the data sources in the following way (first to last priority): the New York Times (Mervosh et al. 2020a), Keystone Strat- egy, a crowdsourcing effort from Stanford and University of Virginia, and Hikma Health. Once a state enacts a policy, the counties inherit the policy of the state. In Appendix Table A1, we provide summary statistics reporting the share of county policies from each source. The distribution of the timing of each county’s first order is shown in Figure 1. We include reopening dates at the state level collected by the NYT (Mervosh et al. 2020b) and curated by Rearc. Additional detail on data construction can be found in Appendix A.1. 2.2 Social Distancing Data The data on social distancing behaviors come from SafeGraph, a data company that aggregates anonymized location data from about 45 million mobile devices and numerous applications in order to provide insights about physical points of interest (POIs). POIs include restaurants, coffee shops, grocery stores, retail outlets, hospitals and many other business establishments. For each POI, SafeGraph reports the daily number of unique device visits along with information on the 2 Desmet and Wacziarg (2020) and Knittel and Ozaltun (2020) examine spatial variation in coronavirus cases and deaths in the United States without employing the framework of an SIRD model. 5 POI’s industry and location.3 For each CSA, we construct the total number of visits to POIs in that CSA for a given day. 2.3 Economic Data Our analysis uses economic data from two sources. We incorporate spending on approximately 10 million debit cards in data from Facteus, a financial data provider that directly partners with banks. This sample consists of traditional debit cards issued by banks, general purpose debit cards issued by merchants, payroll cards issued by employers, and government alimony disbursement cards. Lower- and middle-income individuals are represented more heavily in this data than in the US population. We construct the total number of transactions and dollar amount spent by cards from a given home CSA on a given day.4 We also source information on employment from Homebase, a company providing scheduling and time tracking software to over 60,000 small businesses.5 For each day, we analyze the number of work hours and individuals employed by Homebase partner firms in a given CSA. 2.4 Health Data We pull case and death counts by day at the county level from a continually updated repository by the New York Times that aggregates reports from state and local health agencies. For all dates up to the first available data, we assume no cases nor deaths. We collect state-level testing and hospitalization data from the Covid Tracking Project. 2.5 Demographic Data We supplement the policy and outcome data with data on CSA characteristics. For our measure of partisanship, we use the Republican vote share in the 2016 presidential election (MIT Election Data and Science Lab 2018). Following Allcott et al. (2020), we use the SafeGraph OpenCensus data to assign demographic variables such as race, income, occupation, and commuting to the various geographies analyzed. The SafeGraph OpenCensus data is derived from the 2016 5-year ACS at the census block group level. We add the urban share of the population from the 2010 3 See https://docs.safegraph.com/v4.0/docs/weekly-patterns for additional information on the data’s construction. 4 To protect privacy, Facteus injects a small amount of mathematical noise into key record attributes. This has very minimal impact on aggregate data. More information on this differential privacy procedure can be found at https://www.facteus.com/products/data-products/. 5 Additional information regarding Homebase’s data can be found at https://joinhomebase.com/data/. 6 Census. We also use average seasonal temperatures by geography from Wu et al. (2020), which is ultimately sourced from gridMET (Abatzoglou 2011). To characterize potential global migration flows for transmission, we use flight data from the OpenSky Network (Sch¨afer et al. 2014; Olive 2019). 3 Effects on Social Distancing and Economic Outcomes We first present descriptive evidence of trends in mobility and health by whether a county issued a stay-at-home order on or before March 25, issued an order after March 25, or has yet to issue an order. Panel A of Figure 2 plots trends in the log of average daily POI visits for weeks from January 29, 2020 to May 31, 2020 normalized relative to their January 29, 2020 value. All three of these groups experienced a rapid mobility decrease in March through early April, followed by a more gradual recovery. Counties with an order had somewhat stronger social distancing responses. Panel B of Figure 2 plots trends in the log of average daily new confirmed COVID-19 cases by week and county order timing, normalized relative to the week starting March 25, 2020. Counties with an early order saw a smaller subsequent increase in cases after this normalization week, relative to counties with later or no stay-at-home orders. Figure 3 maps the geographic distribution of social distancing and public policy responses across counties. Panel A shows the percent change in SafeGraph visits from the week beginning January 29, 2020 to that of April 8, 2020, which is the week with the fewest number of POI visits. Panel B visualizes variation in the effective start date of stay-at-home orders across counties. We see a geographic correlation between stronger social distancing and earlier public orders, and both series also correlate with other factors such as population density or virus exposure. Our main results are at the Combined Statistical Area (CSA) by order date level (i.e., we group counties within a CSA who received a stay-at-home order on the same day together) using data from February 1, 2020 to April 30, 2020. We call our unit of observation a “CSA” for simplicity. To estimate the causal effect of these stay-at-home orders, we estimate the following event-study specification k=21 Yit = µi + δt + ∑ ωk 1{t−Ti =k} + εit (1) k=−21,k6=−1 where Yit is the outcome of interest in CSA i during time t, µi is a CSA fixed effect, δt is a date 7 fixed effect, and 1{t−Ti =k} is an indicator for the days relative to the first stay-at-home order Ti .6 Standard errors are clustered at the CSA level irrespective of order timing. Earlier and later time periods are pooled in the k = −21 and k = 21 time indicators respectively. Figure 4 shows clear effects of stay-at-home orders on social distancing and economic out- comes. Panel A shows that a stay-at-home order decreases POI visits by 17.8 percent (se = 1.3) by the day after the order’s effective start date (k = 1). This decrease persists and is relatively stable throughout the window of analysis. Panel B estimates that a stay-at-home order decreases con- sumer debit spending (in total $) by 7.1 percent (se = 0.9) by the day after an order’s effective start date. Panel C estimates an 12.3 percent (se = 1.5) reduction in the number of employees working in our Homebase sample on the day following an order’s implementation. The estimated policy effects are robust to alternative specifications. In Appendix Figure A7 we estimate that a stay-at-home order decreases the number of Facteus debit transactions by 5.7 percent (se = 0.7), the number of total hours in Homebase worked by 13.2 percent (se = 1.6), and the total wages of employees in Homebase by 12.2 percent (se = 1.8) by the day after the order’s effective start date. We show that our results are very similar at the county level in Appendix Figure A3, with analogous estimated decreases of 18.1 percent (se = 1.5) for mobility, 7.3 percent (se = 1.0) for consumer spending, and 12.6 percent (se = 1.3) for employment. In Appendix Figure A6, we estimate much weaker immediate effects from the removal of a stay-at-home order, suggesting a strong asymmetry in treatment effects between the onset and the removal of the order. By the day after an order’s removal, we find increases of 3.7 percent (se = 0.9) for POI visits, 0.9 percent (se = 1.2) for total debit card spending, and 2.4 percent (se = 2.3) for employment. 4 Effects on Health Outcomes 4.1 SIRD Model We start with a discrete-time SIRD model (Kermack and McKendrick 1927), suppressing notation for different geographies i. In outlining this model, we make the assumption that there are no health spillovers across geographies. Furthermore, we abstract from issues around testing and the endogeneity of stay-at-home order timing. 6 For CSAs without a stay-at-home order in our sample, 1{t−Ti =k} is always set to zero. 8 The population is defined by St + It + Rt + Dt = N (2) where St , It , Rt , and Dt are the number of susceptible, infected, recovered, and deceased individuals at time t. Dynamics in the SIRD model are defined by the transition probabilities between states. The laws of motion are given by: It St+1 − St = −βt St (3) N It It+1 − It = βt St − γIt (4) N Rt+1 − Rt = (1 − κ)γIt (5) Dt+1 − Dt = κγIt (6) where βt is the contact rate that governs the speed at which new infections propagate, γ is the rate at which infected individuals recover, and κ is the proportion of recovered individuals that die. We treat the recovery rate γ and death rate κ as fixed parameters during the time period we analyze. Defining the total number of cases to be Ct = It + Rt + Dt and combining equations (4), (5), and (6), we get that new cases evolve as It Ct+1 −Ct = βt St (7) N St We make the simplifying assumption that St ≈ Nt so that we can treat the ratio Nt = 1. As of May 1, less than 0.5 percent of the US population has or had a confirmed case—making this approximation reasonable—though true case count may be greater. This allows us to replace equations (3) and (4) with Ct+1 −Ct = βt It . (8) Furthermore, we can write It = (Ct −Ct−1 ) + (1 − γ)It−1 . (9) Given initial conditions C0 , I0 , the contact rate βt , and the recovery rate γ, equations (8) and (9) 9 define the dynamics of cases over time. 4.2 Estimation Framework A key parameter of interest for policymakers is the contact rate βt . As social distancing increases, the contact rate decreases—yielding fewer new cases. The contact rate βt is proportionally related to the reproduction number R0t as R0t = βt /γ. A proportional effect on the contact rate βt will have the same proportional effect on the reproduction number R0t . We suggest it is natural to think of stay-at-home orders as a proportional effect τ on the contact rate. That is, the contact rate is βt (1 + τ) under a stay-at-home order as opposed to βt . Taking logs of equation (8), we get log(Ct+1 −Ct ) = log(It ) + log(βt ) + log(1 + τTi ). We then use an event-study framework to estimate the impact of treatment Ti k=21 log(Ci,t+1 −Cit ) = α log(Iit ) + δt + ξit + ∑ ωk 1{t−Ti =k} + εit , (10) k=−14,k6=−1 where, relative to equation (1), ξit is an indicator for the non-binned event-study window.7 The ωk coefficients can be interpreted as estimates of τ while δt and ξit control for variation in βt over time unrelated to the policy. Even though It is not directly observed, given initial conditions C0 = I0 and γ, no additional data is required to construct the time-path for It beyond the growth in cases. Below, we use values for γ suggested by the epidemiology literature and examine robustness to alternative values. Note that one test of the model and its assumptions is whether αˆ = 1. In the appendix, we show that this estimator performs well when estimated on data simulated from an SIRD model. 4.2.1 Other Methods of Estimation in the Literature Several previous attempts at estimating the effect of stay-at-home orders have not been model- driven. For example, Dave et al. (2020) use the log of confirmed cases as the outcome in an event- study framework with state-specific linear trends. Lin and Meissner (2020) also use a similar 7 The event-study window indicator is required for normalization when geography fixed effects are excluded. We exclude geography fixed effects because they bias estimates in our simulations. 10 event-study specification with log cases on the left-hand side.8 These estimators can produce unexpected results when the data comes from an SIRD data-generating process. In the appendix, we show that the Dave et al. (2020) estimator exhibits substantial pretrends and fails to recover the estimated treatment effect when estimated on simulated data. We also apply the estimator to real, state-level data as in Dave et al (2020). We qualitatively replicate their results when using the 7-day pre-period event window. When using a more complete 14-day or 21-day pre-period event window, the estimator produces null results with substantial pretrends—mirroring the estimates from this estimator when using data simulated from an SIRD model. To gain intuition for the poor performance of these estimators, equation (8) implies log cases follow log(Ci,t+1 ) = log(βit Iit +Cit ). (11) Therefore, the ωk coefficients from an event study with log cases on the left-hand side are going to pick up differential trends in a nonlinear function of βit , Iit , and Cit across treated and non-treated units rather than differential trends in log(βit ) alone.9 4.3 Results A key input into the estimation process is γ which is the inverse of the average infectious period for COVID-19. We report estimates using a range of values for γ. On one extreme, we set γ = 0 which implies Iit = Cit or an infinite infectious period. On the other extreme, we set γ = 1 which implies an average infectious period of 1 day. Early indications in the literature suggested an infectious period of 4.4 to 7.5 days (Anderson et al. 2020). As of May 8, 2020, the CDC website recommends home isolation until at least 10 days have passed since symptoms first appeared, whereas the UK NHS recommends a minimum of 7 days.10 We view the range of γ = 1/3 (an infectious period of 8 Friedson et al. (2020) use a synthetic control estimator with log cases on the left-hand side to estimate the effect of California’s stay-at-home order. Fowler et al. (2020) and Courtemanche et al. (2020) use a difference-in-difference specification with log(Ci,t+1 ) − log(Cit ) on the left-hand side, which gives log(Ci,t+1 ) − log(Cit ) = log(βit Iit +Cit ) − log(βi,t−1 Ii,t−1 +Ci,t−1 ). Given the nonlinear dynamics of the SIRD model, synthetic control or matching estimates may perform better when the model structure is not accounted for parametrically. 9 Note that even under the simplifying assumption that C = I (which implies γ = 0), rewriting equation (11) still it it gives log(Ci,t+1 ) = log(1 + βit ) + log(Cit ). 10 https://www.cdc.gov/coronavirus/2019-ncov/if-you-are-sick/steps-when-sick.html and https://www.nhs.uk/conditions/coronavirus-covid-19/what-to-do-if-you-or-someone-you-live-with-has- coronavirus-symptoms/staying-at-home-if-you-or-someone-you-live-with-has-coronavirus-symptoms/ 11 three days on average) and γ = 1/12 (an infectious period of twelve days on average) as limits to the range of likely values. Table 2 reports our estimates using case data and stay-at-home orders. To reduce instances where log(Ci,t+1 −Cit ) is undefined, we group counties by the interaction between their cumulative statistical area and the timing of their stay-at-home order.11 We restrict attention to CSA-days with at least 10 cases, the set of CSAs to either never treated CSAs or CSAs which are observed for at least 8 days before and 20 days after the order, and the time period prior to May 1, 2020. Because of the imprecision of the estimates, we estimate an aggregated event study specification (see table notes). In general, γ is positively correlated with the estimated treatment effects of stay-at-home orders on case prevalence. Using likely values of γ, we find a negative estimated effect of stay-at-home orders on case prevalence though these estimated effects have wide confidence intervals. Setting γ = 1/6, which implies an average infectious period of 6 days, our baseline estimates suggest that stay-at-home orders decreased the contact rate βt (i.e., the rate of new cases) by 9.1 percent (se = 4.8) relative to their pre-order levels. Consistent with the data coming from an SIRD data generating process, estimates for α are close to 1. Figure 5 reports the full event-study plot for γ = 0 which sets It = Ct , along with our preferred value of γ = 1/6. The appendix reports the full event studies for the other values of γ. Our estimates come with several caveats. First, there is measurement error in confirmed cases. Adapting the method outlined above, the appendix reports negative point estimates for the effect of stay-at-home orders on the log of new deaths.12 Second, the onset of the stay-at-home orders may be prompted by information that future cases or deaths are likely to exhibit substantial increases. This could lead to upward bias in our estimated effects. On the other hand, stay-at-home orders may be issued in places where people are more likely to respond to the pandemic and so may exhibit higher levels of counterfactual social distancing. 11 For simplicity, we subsequently refer to these CSA-timing groups as CSAs. 12 Note that we can write log(Di,t+1 − Dit ) = log(κγ) + log(1 + βit − γ) + log(Ii,t−1 ) which we can utilize in the same event study framework where ωk are estimates for the impact of the stay-at-home order on log(1 + βit − γ). 12 5 Explaining Variation in Outcomes 5.1 Temporal Variation In this section, we compute the share of the overall change in each outcome during our time period attributable to stay-at-home and business closure orders. Secular trends in the outcomes are prominent over our time period as individuals make voluntary behavioral changes (e.g., Figure 2). To examine the share of aggregate changes explained by policy, we first compute the average total percent reduction in the outcome as YT −Y0 Total∆ = (12) Y0 where Yt is the weighted average of the level of the outcome in week t taken over geographies that enact the corresponding order during our time period, t = 0 is the first week of February, and t = T is the third week of April. We average across days in the week when computing Yt to remove any day-of-week effects.13 Next, we compute the average policy-induced change relative to baseline levels as 1 ωk ×YT (i) Policy∆ = ∑ wi (13) N i Y0 where ωk is the estimated treatment effect from Sections 3 and 4, wi are geography population weights that sum to N, and T (i) is the period prior to the order’s implementation for geography i. We account for uncertainty induced by the estimation of ωk in the standard errors, and treat the values of Yt as given. We set k = 1 in our baseline specification and examine robustness to alternative assumptions. Figure 6 presents the ratio Policy∆/Total∆ for our social distancing, employment, and health outcomes.14 We compute this estimate separately for stay-at-home orders and mandatory business 13 Most CSAs do not have any cases in early February, so the pre-period levels cannot be estimated from the data when examining the overall change in the contact rate βt . Since we must choose γ for each specification and the reproduction number R0 is is βt /γ, we can recover βt in the pre-period by specifying R0 . Anderson et al. (2020) and D’Arienzo and Coniglio (2020) provide an overview of estimates of the initial reproduction rate R0 , ranging from 2.5 to 3.5. Our preferred reproduction rate is R0 = 3.0. We then compute YT and YT (i) using equation (8) and the assumed γ value; we use the assumed R0 when (8) is undefined in our data. 14 Debit card transactions and total spending, according to the Facteus data, did not have a similarly strong decrease between February and April. As a result, the decomposition of this small reduction (or increase in the case of total spending) into a voluntary and mandatory portion is more difficult to interpret. We note that Farrell et al. (2020) find a decrease in consumer spending when using data sources other than Facteus’ debit card panel. 13 closure orders. Table 3 reports Total∆ and Policy∆ individually for the stay-at-home orders, the business closure orders, and the simultaneous implementation of both orders. We estimate that stay-at-home orders explain 16.2 percent of the change in POI visits, 15.6 percent of the change in total wages, 16.0 percent of the change in total employment, and 13.1 percent of the change in the contact rate βt when setting γ = 1/6 and R0 = 3.0. Overall, while stay-at-home orders only explain a small proportion of the overall changes in social distancing and case growth, they do not appear inefficient. Stay-at-home orders have a wage cost per unit of social distancing that is 0.96 times as large as the average cost across voluntary behavioral changes and other government orders and has a relative employment cost that is 0.99 times as large.15 In contrast to the stay-at-home orders, the employment cost per unit of social distancing for business closures is relatively high. Our estimates suggest that business closure orders have a wage cost per unit of social distancing that is 2.25 times larger than the average cost across voluntary behavioral changes and other government orders and has a relative employment cost that is 1.91 times greater.16 It is important to note that these cost-benefit comparisons are necessarily restrictive and do not account for all economic and health factors associated with the policies. Moreover, we analyze short-run cost-benefits and the long-run implications of policy may be different. In Appendix Table 4, we also consider the case where we set k = 20 for estimating the treat- ment effects or where we estimate treatment effects from fitting a linear pretrend in the two weeks prior to the order’s implementation and computing the estimated treatment effect as the difference between the extrapolated pretrend and the treatment effect at k = 20.17 The qualitative conclu- sions regarding the relative efficiency of stay-at-home orders is unchanged across these alternative estimators. 5.2 Geographic Variation We next examine factors that explain the geographic variation in health outcomes. Table 1 reports summary statistics for all CSAs, CSAs with above median average contact rates, and CSAs with below median average contact rates. It also reports the difference between the above- and below-median groups. CSAs with above median contact rates actually exhibited 15 That is, .156 1−.156 .160 1−.160 .162 / 1−.162 = 0.96 and .162 / 1−.162 = 0.99. 16 That .182 1−.182 is, .090 / 1−.090 = 2.25 and .159 1−.159 .090 / 1−.090 = 1.91. 17 In computing the standard errors for this specification, we account for the additional variance induced by the extrap- olation by adding the variance from the predicted value from the linear fit. 14 larger decreases in POI visits and were under stay-at-home orders for longer than CSAs with below median contact rates, though these differences are statistically insignificant and may reflect endogenous changes. The primary difference between the two groups are that CSAs with above median contact rates have denser, more urban, and larger populations. They also commute by automobile less, have more international flights passing through, are more Democratic, and are more educated. To formalize the comparison across CSAs, we extend our parameterization of the contact rate βit as a function of social distancing behaviors along with date and CSA fixed effects log(βit ) = Λ0 ∆ log(POIit ) + θi + ρt + νit (14) where ∆ log(POIit ) is the change in the log of POI visits between March 1, 2020 and t, θi are CSA fixed effects, ρt are date fixed effects, and νit are unobserved by the econometrician. We use our constructed series for Iit and the case growth Ci,t+1 −Cit to define βit as in equation (8) assuming γ = 1/6. Note that we can use the ratio of the treatment effects of stay-at-home orders on social distancing behaviors in Section 3 and on the contact rate from Table 2 to provide a causal estimate ˆ 0 for the change in the contact rate per change in social distancing. Constraining Λ0 to be the Λ estimated ratio from our event-study specifications, we estimate equation (14) via a fixed effects estimator.18 Table 4 reports the average difference in log contact rates log(βit ) across various groups of CSAs with high and low average case growth. To understand the role of social distancing and policy in explaining differences between these groups, we use equation (14) and our previous event-study estimates to obtain the predicted log contact rates if (i) stay-at-home policies were equated across all CSAs and (ii) if changes in social distancing were equated across all CSAs. Our estimates suggest that little to none of the average geographic variation in log contact rates can be explained by differences in social distancing behaviors or policy. The timing of virus onset, accounted for by ρt , does little to explain these averages differences either.19 Consistent with Table 1, these results suggest the vast majority of differences across CSAs are 18 To 1 1 implement the regression constraint and avoid taking the log of zero, we set βik = 1,000,000 when βik < 1,000,000 and we estimate ˆ 0 ∆ log(POIit ) = θi + ρt + νit log (βit ) − Λ where we use the same estimating sample as in Section 4 restricted to the period between March 15 and April 30, 2020, and we set Λˆ 0 = .091 = .51. We do not use population weights. .178 19 Appendix Table A3 reports the share of the cross-CSA variance in log contact rates log(β ) explained by each set it of covariates and provides similar conclusions as the additive decomposition in Table 4. 15 driven by the estimated fixed effects θi . What, however, explains the geographic variation in fixed effects? To examine the determinants of these fixed differences across CSAs, we first perform the de- scriptive exercise of regressing the CSA fixed effects θi on CSA-level covariates using OLS. Panel A of Figure 7 shows the standardized coefficient estimates from univariate regressions. Panel B of Figure 7 shows the corresponding coefficients when controlling for log population. While many variables are significant predictors in the univariate regressions, only racial composition (share Black, Asian, and Other) and partisanship (Republican vote share) are significant predictors after controlling for log population. Next, we formalize the prediction exercise using the full set of covariates and lasso to select and penalize coefficients.20 We choose the lasso penalty to maximize out-of-sample fit in a 10-fold cross-validation without using population weights. Lasso selects variables that cover population (log population and log population density), racial composition (share Black and Other), and par- tisanship (Republican vote share). Figure 8 shows the fit of the predicted fixed effects from the lasso regression and the estimated fixed effects θˆi . Overall, the model performs well—accurately predicting the contact rate fixed effect for NYC and other major CSAs but performing less well on smaller CSAs. Using the lasso estimates, we return to the additive decomposition in Table 4. We recompute the log contact rates after equating various subsets of covariates using the estimated coefficients from our lasso model. Overall, the covariates in our lasso model explain 55 percent of the differ- ence between CSAs with above-median case growth and CSAs with below-median case growth. The population variables, log population and log population density, are the primary predictors— explaining 48 percent of the above-below median difference in CSAs by themselves with partisan- ship explaining smaller shares. These results suggest fixed differences across locations played a larger role in explaining dif- ferential case growth early on in the pandemic than policy or observed social distancing behaviors. Predictors and drivers of temporal or geographic variation later in the pandemic may be different. The S = N assumption is also less tenable during later periods in the pandemic as the recovered population grows—thus, complicating an analysis of this later period. 20 We exclude the log number of tests as of April 30th from the lasso exercise for endogeneity reasons. 16 5.3 Counterfactuals Finally, we conduct several counterfactual exercises. Our exercises take the form of constructing alternate sequences of contact rates {βik }tk=0 and using the SIRD model outlined above to compute counterfactual cases given observed initial conditions I0 = C0 .21 In Figure 9, we compute various counterfactual contact rate sequences {βikc }tk=0 and examine how these alternative sequences would have shaped the evolution of total cases in our sample. Assuming a proportional impact of stay-at-home orders on social distancing behaviors as estimated in Section 3, a uniform stay-at-home order implemented on March 17 (when the San Francisco Bay Area implemented their stay-at-home order) would have resulted in 154,000 fewer cases by April 30th, or a 19.5 percent reduction in cases.22 If, instead, we assume that stay-at-home orders cause social distancing behaviors to fall to a fixed level at 35 percent of baseline levels, a uniform stay- at-home order implemented on March 17 would have resulted in 494,000 fewer cases, or a 62.5 percent reduction in cases. If all CSAs followed the social distancing behaviors of the counties in the San Francisco Bay Area that were the first to initiate stay-at-home orders, there would be 349,000 fewer cases in our sample, or a 44.1 percent reduction. Lastly, removing the proportional effect of all policy would have resulted in 494,000 more cases, or a 62.4 percent increase in cases. While policy explains a small proportion of the temporal variation in case growth and an even smaller proportion of the geographic variation, policy still has led to a non-trivial reduction in cases. As of September 4, 2020, the observed case fatality rate in the United States was 3 percent.23 Based on this observed case fatality rate, the stay-at-home policies saved 14,800 lives and a further 10,500 lives could have been saved if all CSAs followed the social distancing behavior of the counties in the San Francisco Bay Area that were the first to initiate stay-at-home orders during the initial period of the pandemic. 6 Conclusion We use event studies and a model-driven regression framework to provide new decompositions on the role of policy in driving the spatial and temporal variation in case transmission during the early months of the coronavirus pandemic. We find that policy was responsible for roughly 15 percent 21 We 1 restrict βik ≥ 1,000,000 . 22 To implement, we counterfactually reduce the log of POI visits by .178 after March 17 for CSAs not under an order at that time. 23 See https://coronavirus.jhu.edu/data/mortality accessed on September 4, 2020. 17 of the change in virus contact rates between early March and mid-April. Moreover, policy explains little-to-none of the differences in average contact rates between CSAs with high- and low-contact rates. Rather, the most important predictors of which cities were hardest hit by the pandemic are exogenous characteristics such as population and density. These results inform the debate about the role of policy in the initial months of the coronavirus pandemic. While our results suggest they explain a small proportion of the overall spatial and temporal variation, this does not mean that (a) policy is inefficient or (b) policy is not important. 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Working Paper. 21 Figure 1: Distribution of Timing of First Government Order 1.5e+05 Number of Counties 1.0e+05 5.0e+04 0 Mar 4 Mar 11 Mar 18 Mar 25 Apr 1 Apr 8 Date of Order Stay-at-home order Business closing order Note: Figure shows the distribution of government order effective start dates over time and across counties. Each bar represents the number of counties (y-axis) for which the first order of a given type went into effect on the date specified (x-axis). Stay-at-home and business closing orders are shown in blue and orange bars respectively. See Section 2.1 for detail on data sources and processing. 22 Figure 2: Trends in Average Mobility and Health Panel A: Mobility 0.0 Normalized Log(Visits) −0.4 Timing Early Order Late Order No Order −0.8 −1.2 Fe Ma Ap Ma Ju n b r y r Week Panel B: Health 2 Normalized Log(New Cases) 0 Timing Early Order Late Order No Order −2 Fe Ma Ap Ma Ju n b r y r Week Note: Figure reports trends in average mobility and health by county order timing and week. Panel A plots the log of daily average POI visits, normalizing relative to the week starting January 29, 2020. Panel B plots the log of daily new COVID-19 cases, normalized to the week starting March 25, 2020. In both panels, averages are weighted by population and taken across counties and days prior to taking logs or normalization. ‘Early Order’ indicates counties with a stay-at-home order on or before March 25, 2020. ‘Late Order’ indicates counties with a stay-at-home order after this point. ‘No Order‘ indicates counties which did not issue a stay-at-home order during this sample period. The dashed vertical line indicates the week starting March 25, 2020. 23 Figure 3: Geographic Variation in Social Distancing and Public Policy Panel A: % Change in SafeGraph Visits (-45,38] (-51,-45] (-56,-51] (-63,-56] [-96,-63] No data Panel B: Shelter-in-Place Order Effective Start Date [12mar,24mar] (24mar,26mar] (26mar,30mar] (30mar,02apr] (02apr,07apr] No identified order Note: This figure shows the U.S. geographic distribution of social distancing and public policy responses. Panel A shows for each county the percent change in aggregate visits between the week beginning January 29, 2020 and the week beginning April 8, 2020. Blue shading denotes a more negative percent change in visits during the latter week relative to the former. Red shading indicates an increase or a smaller decrease in visits. These visits are sourced from SafeGraph’s mobile device location data. Panel B shades U.S. counties by the effective start date for the earliest shelter-in-place order issued (see Section 2.1 for sources). Blue shading indicates an earlier order, while red shading indicates that an order was issued later or was never issued. 24 Figure 4: Effect of Stay-at-Home Orders on Mobility and Economic Outcomes Panel A: Effect on Mobility 0.40 0.20 Coefficient Estimate 0.00 -0.20 -0.40 -21 -14 -7 0 7 14 21 Days Relative to Order Panel B: Effect on Consumer Spending 0.40 0.20 Coefficient Estimate 0.00 -0.20 -0.40 -21 -14 -7 0 7 14 21 Days Relative to Order Panel C: Effect on Employment 0.40 0.20 Coefficient Estimate 0.00 -0.20 -0.40 -21 -14 -7 0 7 14 21 Days Relative to Order Note: Figure plots estimated treatment effects ωk of stay-at-home orders on different outcomes, using the event-study specification outlined in equation (1) at the CSA-day level. Panel A shows the effect on mobility, using the log of total POI visits in SafeGraph data. Panel B shows the effect on consumer spending, using the log of total spending in Facteus’ debit card sample. Panel C shows the effect on employment, using the log number of individuals with positive work hours from the Homebase sample. All regressions include CSA fixed effects µi and date fixed effects δt . CSAs are weighted by population in the regression. Standard errors are clustered at the CSA level irrespective of order timing. 25 Figure 5: Effect of Stay-at-Home Orders on Health Outcomes Panel A: Log New Cases, Model Free 1.00 0.75 0.50 Coefficient Estimate 0.25 0.00 -0.25 -0.50 -0.75 -1.00 -14 -7 0 7 14 21 Days Relative to Order Panel B: Contact Rate (γ = 1/6) 1.00 0.75 0.50 Coefficient Estimate 0.25 0.00 -0.25 -0.50 -0.75 -1.00 -14 -7 0 7 14 21 Days Relative to Order Note: Figure plots estimated treatment effects ωk from the event-study specification outlined in equation (15) using the log of new cases in a CSA for a given day as the outcome. Panel A includes date fixed effects δt , the event window indicator ξit , and sets γ = 0 which implies log(Iit ) = log(Cit ). Panel B is the same as Panel A, except that it sets γ = 1/6. CSAs are weighted by population in the regression. Standard errors are clustered at the CSA level irrespective of order timing. 26 Figure 6: Temporal Variation Explained by Policy Panel A: Social Distancing and Employment Outcomes 0.25 0.20 Policy-Induced Share 0.15 0.10 0.05 POI Visits Wages Employment Stay-at-Home Business Panel B: Contact Rate βt 0.8 0.6 Policy-Induced Share 0.4 0.2 0.0 γ=1/6 γ=1/9 γ=1/12 Contact Rate (β) R0=2.7 R0=3 R0=3.3 Note: Figure plots the share of the total change in each outcome that is attributable to a given policy Policy∆/Total∆ following Section 5.1. Panel A reports estimates using stay-at-home orders and business closure orders for POI visits from SafeGraph, total wages from Homebase, and employment from Home- base. For each policy treatment, we restrict attention to the CSAs treated by the given policy. Panel B reports estimates of the policy-induced change in the contact rate βt from stay-at-home orders. In both panels, the bars depict 95 percent confidence intervals. See Table 3 for additional details. 27 Figure 7: Determinants of Geographic Variation in Log Contact Rates Panel A: Univariate Regression of θˆi on Covariates Log Pop. Log Pop. Density Frac. Urban Share 4-year Degree Share Hispanic Share Race - Other Share Race - Asian Share Race - White Share Race - Black Share Age <18 Share Age ≥65 Republican Vote Share Log International Flights Share Commute by Car Avg. Summer Temp. Avg. Winter Temp. Log Tests -.75 -.5 -.25 0 .25 .5 .75 Standardized Coefficient Panel B: Controlling for Log Population Log Pop. Log Pop. Density Frac. Urban Share 4-year Degree Share Hispanic Share Race - Other Share Race - Asian Share Race - White Share Race - Black Share Age <18 Share Age ≥65 Republican Vote Share Log International Flights Share Commute by Car Avg. Summer Temp. Avg. Winter Temp. Log Tests -.75 -.5 -.25 0 .25 .5 .75 Standardized Coefficient Note: Figure plots the coefficients of regressing the CSA log contact rate fixed effect estimates θˆi from equation (14) on CSA-level determinants. The θˆi and all covariates have been standardized to have a mean 0 and a standard deviation of 1. Panel A plots the standardized coefficients and 95 percent confidence intervals from univariate regressions. Panel B repeats Panel A but the regressions also control for the log of population. Population weights are not used. Robust standard errors are used to compute the confidence intervals. 28 Figure 8: Model Fit for Average Log Contact Rates, Full Lasso Model 2 Boston Philly Chicago LA Cleveland DC Miami Detroit Denver NYC SF Atlanta Minneapolis Orlando Portland Charlotte Dallas Seattle Houston 0 Estimated Log Contact Rate FE −2 −4 −1 0 1 Predicted Log Contact Rate FE Note: Figure plots predictions of the estimated fixed differences in CSA log contact rates θˆi in OLS re- gressions using γ = 1/6. The plotted points are sized proportional to CSA population and the top 25 most populous CSAs are filled in and labeled. In this figure, the fixed effects are averaged using population weights and the population is summed across order timings when a CSA has multiple order timings. The solid line is a 45 degree line indicating perfect prediction and the dashed line is a linear fit of the estimated fixed effects on their predictions for the CSAs plotted. We drop two observations when plotting to focus on the variation across the majority of CSAs. 29 Figure 9: Counterfactual Cases 1.5 1 Cases (millions) .5 0 Mar 1 Mar 15 Mar 29 Apr 12 Apr 26 No Policy - Proportional Observed March 17 Policy - Proportional SF Distancing March 17 Policy - Fixed Note: Figure plots observed and counterfactual cases following the methodology outlined in Section 5.3 for our sample of cumulative statistical areas (CSAs) using γ = 1/6. Figure reports the observed number of cases along with the estimated number of cases if a uniform stay-at-home order was implemented on March 17 with proportional effect on social distancing behaviors, a uniform stay-at-home order was implemented on March 17 that caused social distancing behaviors to fall to a fixed level of 35 percent of March 1 levels, and the estimated number of cases if all areas followed the same social distancing behavior as the San Francisco Bay Area (defined to be the counties in the San Francisco CSA that were first to implement a stay-at-home order). 30 Table 1: CSA Summary Statistics All Above Med. Below Med. Difference Contact Rate Contact Rate Log Contact Rate (βt , γ = 1/6) -2.259 -1.617 -2.901 1.285 (1.230) (0.138) (1.482) [0.914, 1.668] Log Cases per 100,000 on April 30 5.100 5.403 4.798 0.605 (0.894) (0.820) (0.869) [0.288, 0.876] Log Deaths per 100,000 on April 30 1.738 2.154 1.308 0.846 (1.203) (1.178) (1.078) [0.368, 1.195] Log POI Visits 10.545 11.137 9.953 1.184 (1.125) (0.947) (0.971) [0.828, 1.555] ∆Log POI Visits -0.642 -0.658 -0.626 -0.032 (0.219) (0.193) (0.242) [-0.099, 0.053] Share of Days with Order 0.650 0.697 0.603 0.094 (0.271) (0.232) (0.299) [-0.013, 0.186] Log Pop Density 6.044 6.836 5.252 1.584 (1.501) (1.447) (1.083) [1.101, 2.035] Log Population 13.436 14.114 12.758 1.356 (1.192) (1.018) (0.947) [0.999, 1.712] Share Urban 0.821 0.881 0.761 0.120 (0.181) (0.153) (0.188) [0.070, 0.196] Average Summer Temperature 88.440 87.480 89.400 -1.920 (5.215) (5.413) (4.867) [-3.525, 0.200] Average Winter Temperature 50.292 50.386 50.198 0.187 (12.432) (13.712) (11.125) [-4.010, 5.249] Share Commute Auto 0.887 0.864 0.910 -0.045 (0.076) (0.096) (0.038) [-0.069, -0.019] Log International Flights 2.759 4.297 1.222 3.075 (3.084) (3.280) (1.901) [1.973, 4.093] Republican Vote Share 0.491 0.445 0.538 -0.093 (0.152) (0.140) (0.151) [-0.150, -0.043] Share Age ≥ 65 0.145 0.142 0.147 -0.005 (0.039) (0.041) (0.037) [-0.020, 0.009] Share Black 0.157 0.163 0.150 0.014 (0.143) (0.129) (0.156) [-0.035, 0.067] Share White 0.741 0.721 0.762 -0.040 (0.148) (0.135) (0.158) [-0.101, 0.012] Share with Bachelor’s or More 0.304 0.328 0.280 0.047 (0.090) (0.077) (0.095) [0.014, 0.082] Note: Table reports summary statistics of the average CSA covariate values between March 15 and April 30, except for cases and deaths which the April 30th values are used. The means across all CSAs and the grouped CSAs by average log contact rate log(βt ) using γ = 1/6 are reported along with bootstrapped standard errors. The difference-in-means between the top and bottom contact rate groups are reported along with bootstrapped 95 percent confidence intervals. Statistically significant difference-in-means are bolded. ‘∆Log Visits’ reports the change in log POI visits relative to March 1, 2020. ‘Share of Days with Order’ reports the share of the March 15–April 30 time period in which a CSA is under a stay-at-home order. 31 Table 2: Estimated Effects of Stay-at-Home Orders on Contact Rate (1) (2) (3) (4) (5) γ =0 γ = 1/12 γ = 1/9 γ = 1/6 γ = 1/3 Post-order -0.203 -0.139 -0.121 -0.091 -0.023 (0.086) (0.060) (0.055) (0.048) (0.045) log(Iit ) 1.053 1.048 1.044 1.037 1.013 (0.027) (0.019) (0.017) (0.012) (0.006) Clusters 76 76 76 76 76 Obs. 5240 5240 5240 5240 5240 Note: Table shows estimated coefficients from estimating an aggregated version of the event study in equa- tion (1): log(Ci,t+1 −Cit ) = α log(Iit ) + δt + ω0 Eit + ω1 Postit + ξit0 + ξit1 + εit (15) where Eit = 1{−9<t−Ti <21} , Postit = 1{−1<t−Ti <21} , ξit0 = 1{t−Ti <−8} , and ξit1 = 1{t−Ti >20} . ‘Post-order’ reports ωˆ 1 , and ‘log(Iit )’ reports α. ˆ Each column reports estimates for a different value of γ as reported in the header. Observations are weighted by population. Standard errors clustered by CSA are reported in parenetheses. 32 Table 3: Role of Policy in Explaining Aggregate Temporal Changes in Distancing, Economic, and Health Outcomes Panel A: Social Distancing and Economic Outcomes (1) (2) (3) Stay-at-Home Business Both Orders Total Policy Total Policy Total Policy POI Visits -0.672 -0.109 -0.665 -0.060 -0.700 -0.178 (0.008) (0.011) (0.018) Homebase Wages -0.590 -0.092 -0.577 -0.105 -0.582 -0.183 (0.013) (0.023) (0.039) Homebase Employment -0.592 -0.095 -0.584 -0.093 -0.620 -0.170 (0.012) (0.017) (0.038) Facteus Debit Transactions 0.048 -0.055 0.056 -0.017 -0.003 -0.057 (0.007) (0.007) (0.013) Facteus Total Spending 0.284 -0.071 0.302 -0.012 0.195 -0.069 (0.009) (0.010) (0.017) Panel B: Contact Rate βt (1) (2) (3) γ = 1/12 γ = 1/9 γ = 1/6 Total Policy Total Policy Total Policy R0 = 2.7 -0.574 -0.245 -0.610 -0.172 -0.634 -0.098 (0.107) (0.078) (0.052) R0 = 3.0 -0.617 -0.221 -0.649 -0.155 -0.670 -0.088 (0.096) (0.070) (0.047) R0 = 3.3 -0.652 -0.201 -0.681 -0.141 -0.700 -0.080 (0.087) (0.064) (0.042) Note: Table reports the total and policy-induced changes in various outcomes as outlined in Section 5.1. In Panel A, we consider the policy-induced changes of stay-at-home orders, business closures, and simultane- ous stay-at-home and business closures. Each column restricts attention to the set of CSAs that receive a given treatment, with Column (3) restricting to counties in which business closure and stay-at-home orders went into effect on the same day. The treatment effects ωk used in Panel A set k = 1. In Panel B, all specifi- cations estimate the effect of stay-at-home orders using estimates from the CSA level and use the estimated treatment effect ωk from Table A1. 33 Table 4: Additive Decomposition for Differences in Log Contact Rates Above/Below Med. Top/Bot. Quart. Top/Bot. Dec. Overall Difference 1.228 2.171 3.565 Share of difference explained by: Social Distancing -0.009 -0.010 -0.023 Policy -0.006 -0.007 -0.007 Timing of Virus -0.000 -0.003 -0.003 Observed Covariates 0.548 0.508 0.424 Population 0.482 0.423 0.336 Climate 0.000 0.000 0.000 Transport 0.000 0.000 0.000 Race -0.036 -0.015 -0.023 Partisanship 0.103 0.100 0.110 College Degrees 0.000 0.000 0.000 Age Demographics 0.000 0.000 0.000 Note: Table reports the difference in the average log contact rate log(βit ) between March 15 and April 30, 2020 for each group of CSAs. It also reports the counterfactual share of the overall difference explained by each set of determinants as outlined in Section 5.2. 34 A Appendix See the replication code for exact details on data construction and estimation. A.1 Data Construction Procedures We construct the datasets used in our analysis as follows. 1. We begin by matching SafeGraph POIs to the counties in which they are located. We use latitude and longitude from SafeGraph’s August 2020 Core POI dataset, along with the 2010 TIGER county shapefile.24 We successfully assign 99.9 percent of the POIs to a county. 2. We then merge the POI-county mapping from (1) onto SafeGraph’s Patterns data using the safegraph-place-id variable. We sum visits by county for a given day, aggregating across POIs. Our SafeGraph series ranges from January 1, 2020 to August 30, 2020. 3. We then merge onto the output from (2) a dataset of county-level demographic information constructed as follows. We use the Open Census data from SafeGraph, aggregating up the data given at the census block group level to the county level. We combine this with data on county 2016 Presidential votes shares (MIT Election Data and Science Lab 2018). We define the Republican vote share to be the share of votes received by the Republican candidate over the sum of votes across all candidates. We exclude counties without valid vote data, which drops Alaska and two additional counties (FIPS: 15005, 51515). We also merge on the urban population share from the 2010 Census.25 We also use average seasonal temperatures by geography from Wu et al. (2020), which is ultimately sourced from gridMET. Averages for a given county and season are taken across the years 2010-2016. 4. We then merge onto the output from (3) the number of incoming international flights for each US county from December 2019 to February 2020 made available by the OpenSky Network (Sch¨afer et al. 2014; Olive 2019). 5. We then merge data on Covid-19 health outcomes onto the output from (4). We source confirmed Covid-19 cases and deaths by county and day from The New York Times. We assume zero cases and deaths for the observations not observed in The New York Times data. We drop the four counties which overlap with Kansas City (MO), because The New York Times lists these as geographic exceptions where it either does not assign cases to these counties or excludes cases occurring within the city. For the five boroughs of New York City, 24 Downloadedfrom https://www.census.gov/geo/maps-data/data/cbf/cbf counties.html on July 24, 2018. 25 Downloaded from https://www.census.gov/programs-surveys/geography/technical-documentation/records- layout/2010-urban-lists-record-layout.html on June 25, 2020. 35 we assign cases and deaths based on their population share. We also merge data on testing and hospitalizations from the Covid Tracking Project, by state and day. 6. We then merge a dataset of county-level shelter-in-place and business closure order start dates onto the output from (5) and construct an indicator for whether a county had been subject to a shelter-in-place and/or business closure order by a given date. It is ultimately sourced from The New York Times, Keystone Strategy, a crowdsourcing effort from Stanford University and the University of Virginia, and Hikma Health. The New York Times has been tracking “shelter-in-place”, “stay-at-home”, “healthy-at-home”, etc. policies enacted at the city, county and state level (Mervosh et al. 2020a). We use the dates reported by the NYT for our stay-at-home policy. The relevant NPIs from Keystone’s data are shelter- in-place (SIP) and closure of public venues (CPV) policies. Keystone considers an “order indicating that people should shelter in their home except for essential reason” as a SIP intervention and a “government order closing gathering venues for in-person services” as a CPV intervention. We will use Keystone’s SIP and CPV dates for our stay-at-home and business closure policies respectively. The crowdsourced data collected by a group from Stanford and University of Virginia solicits policy and personal information from survey participants in an online form. We use the “lockdown” and “business closed” dates for counties from this data. Hikma Health, a non-profit working on data systems and analysis for healthcare providers, has carried out their own crowdsourcing effort to document NPIs. We use the county “shelter date” and “work date” from Hikma Health in our construction of stay-at-home and business closure policies respectively. Given that none of the sources have entirely overlapping policy data, we define both our stay-at-home and business closure policies by sequentially assigning enforcement dates when data is available in the order: NYT, Keystone, Stanford/Virginia crowdsource, and Hikma Health. Once a state enacts a policy, the counties inherit the policy of the state. We then merge on a dataset of reopening dates at the state level collected by the NYT (Mervosh et al. 2020b) and curated by Rearc. 7. We then merge on debit card transactions and spending totals from Facteus onto the output from (6). Prior to this merge, Facteus data is aggregated from the zip code to the county level using a 5-digit zip code to county crosswalk downloaded from HUD (https://www.huduser.gov/portal/dataset on April 12, 2020. Facteus data ranges from Jan 1, 2020 to August 27, 2020, with missing data on August 7, 2020. 8. We then merge on employment data from Homebase onto the output from (7). Homebase data is aggregated to the county-day level prior to this merge. This step completes the con- struction of the dataset used in our county-level analysis. Homebase data ranges from Jan 1, 2020 to August 31, 2020. 36 9. For analysis at the level of a CSA, order date, and day, we then aggregate the output from (8) to this level. We use a county to CSA crosswalk downloaded on May 29, 2020 from the NBER (http://data.nber.org/cbsa-csa-fips-county-crosswalk/cbsa2fipsxw.csv), which uses de- lineation files originally sourced from the Census. We sum countable variables such as POI visits or Covid-19 cases. For other variables, we take a population-weighted average across counties in a CSA-day with the same social distancing policy start date. In our CSA-level analysis, we exclude counties not assigned to a CSA. A.2 SIRD Simulations and Estimation Details A.2.1 Simulation To generate data from an SIRD data generating process, we assume a death rate κ = .008 and an average infectious period of 10 days (γ = .1). We assume βit evolves as βit = γ(Ri0 eλit + R1 (1 − eλit )) × (1 + τTit ) where Ri0 is drawn from a normal distribution with mean of 2.4 and standard deviation of 0.1, R1 = .95, τ is either 0 or -0.1 depending on the simulation, Tit is drawn from a binomial distribution with size 150 and probability 4/15, and λ is drawn from a normal distribution with mean −0.08 and standard deviation 0.01. The exponential decay process for βt follows Fern´andez-Villaverde and Jones (2020). The initial share of the population infected is drawn from an exponential distribution with rate 10, 000. The size of the population is drawn from an exponential with rate 1/100, 000. We then follow the laws of motion outlined in the main text, updating βt each period. Note that in constructing the simulations, we do not use the S/N ≈ 1 assumption but simulate data from the complete model. We simulate data for 200 geographies with 150 time periods. We then follow the estimation process outlined in the main text and assume that γ is the true value used in simulations. We drop the event window indicator in equation (15) when including geography fixed effects. We also show robustness to incorrectly specifying τ as half its true value and twice its true value. A.2.2 Dave et al. (2020) Dave et al. (2020; Figure 4) use an event-study specification with the log of confirmed cases on the left-hand side and geography-specific linear time trends, e.g., k=21 log(Cit ) = µi + µi × t + δt + ∑ ωk 1{t−Ti =k} + εit (16) k=−7,k6=−1 37 where log(Cit ) is the log of confirmed cases in geography i during time t, µi is a geography fixed effect, δt is a date fixed effect, 1{t−Ti =k} is an indicator for the days relative to the first stay-at-home order Ti , and µi × t is a geography-specific linear time trend.26 Following Dave et al. (2020), we exclude data after April 20, 2020. A.2.3 Estimation Details To implement our SIRD estimator, we proceed as follows: 1. We assume zero cases in counties for which none have been reported, aggregate county data to the CSA-order timing level (subsequently “CSA”), and constrain cumulative cases to be non-decreasing at the CSA level. We then make the following restrictions: (a) CSA-days with at least 10 cases, (b) CSAs that either never receive a stay-at-home order or are observed at least 8 days prior and 20 days after the implementation of the order, and (c) CSA-days between February 1, 2020 and April 30, 2020. 2. We set Ci0 to be the number of confirmed cases during the period in which at least 10 cases are confirmed, and we define Ci0 = Ii0 . 3. We then use equation (9) to define the full time path of Iit for each geography given γ. 4. We then estimate equation (15), using log( 21 + Ct+1 − Ct ) to avoid taking log of zero when no new cases are observed. 26 In their event-study specification, Dave et al. (2020) aggregate multiple post-treatment periods into a single treatment effect and include other control variables. 38 Appendix Figure A1: Relative Timing of Stay-at-Home Orders 1.0 Fraction With a Stay-at-Home Order 0.8 0.6 0.4 0.2 0.0 -20 -10 0 10 20 Days Relative to 0.01% of Population Infected Note: Figure plots the population weighted share of counties with a stay-at-home order relative to the point in time in which at least 0.01% of the population has a confirmed case. 39 Appendix Figure A2: Distribution of Stay-at-Home Order Removal Timing 1500 1000 Number of States 500 0 Apr 22 Apr 29 May 6 May 13 May 20 May 27 Jun 3 Jun 10 Note: Figure shows the distribution of state reopenings. Each bar represents the number of states that initiated the removal of their stay-at-home order on the corresponding date. See Section 2.1 for detail on data sources and processing. 40 Appendix Figure A3: Effect of Stay-at-Home Orders at the County Level Panel A: Effect on Mobility 0.30 0.20 Coefficient Estimate 0.10 0.00 -0.10 -0.20 -0.30 -21 -14 -7 0 7 14 21 Days Relative to Order Panel B: Effect on Consumer Spending 0.30 0.20 Coefficient Estimate 0.10 0.00 -0.10 -0.20 -0.30 -21 -14 -7 0 7 14 21 Days Relative to Order Panel C: Effect on Employment 0.30 0.20 Coefficient Estimate 0.10 0.00 -0.10 -0.20 -0.30 -21 -14 -7 0 7 14 21 Days Relative to Order Note: Figure plots estimated treatment effects ωk of stay-at-home orders on different outcomes, using the event-study specification outlined in equation (1) at the county-day level. Panel A shows the effect on mobility, using the log of total POI visits in SafeGraph data. Panel B shows the effect on consumer spending, using the log of total spending in Facteus’ debit card sample. Panel C shows the effect on employment, using the log number of individuals with positive work hours from the Homebase sample. All regressions include county fixed effects µi and date fixed effects δt . Counties are weighted by population in the regression. Standard errors are clustered at the state level irrespective of order timing. 41 Appendix Figure A4: Effect of Mandatory Business Closure or Simultaneous Orders Panel A: Effect on Mobility Business Closure Combined Business Closure and Stay-at-Home 0.40 0.40 0.20 0.20 Coefficient Estimate Coefficient Estimate 0.00 0.00 -0.20 -0.20 -0.40 -0.40 -21 -14 -7 0 7 14 21 -21 -14 -7 0 7 14 21 Days Relative to Order Days Relative to Order Panel B: Effect on Consumer Spending Business Closure Combined Business Closure and Stay-at-Home 0.40 0.40 0.20 0.20 Coefficient Estimate Coefficient Estimate 0.00 0.00 -0.20 -0.20 -0.40 -0.40 -21 -14 -7 0 7 14 21 -21 -14 -7 0 7 14 21 Days Relative to Order Days Relative to Order Panel C: Effect on Employment Business Closure Combined Business Closure and Stay-at-Home 0.40 1.20 0.80 0.20 Coefficient Estimate Coefficient Estimate 0.40 0.00 0.00 -0.40 -0.20 -0.80 -0.40 -1.20 -21 -14 -7 0 7 14 21 -21 -14 -7 0 7 14 21 Days Relative to Order Days Relative to Order Note: Figure plots estimated treatment effects ωk of policy orders on different outcomes, using the event-study speci- fication outlined in equation (1) at the CSA-day level. ‘Business Closure’ subfigures analyze event studies of business closure orders. ‘Combined Business Closure and Stay-at-Home’ restricts to CSAs that implement their business clo- sure and stay-at home orders at the same time. Panel A shows the effect on mobility, using the log of total POI visits in SafeGraph data. Panel B shows the effect on consumer spending, using the log of total spending in Facteus’ debit card sample. Panel C shows the effect on employment, using the log number of individuals with positive work hours from the Homebase sample. All regressions include CSA fixed effects µi and date fixed effects δt . CSAs are weighted by population in the regression. Standard errors are clustered at the CSA level irrespective of order timing. 42 Appendix Figure A5: Heterogeneity in Effect of Stay-at-Home Orders on Social Distancing by Order Date 0.1 Slope: 0.0021 (0.0034) 0.0 Estimate of ω1 -0.1 -0.2 -0.3 -0.4 Mar 16 Mar 21 Mar 26 Mar 31 Apr 5 Date of Stay-at-Home Order Note: Figure plots estimated treatment effects ω1 from the event-study specification outlined in equation (1), run separately by date of the stay-at-home order, using the log of total POI visits in a CSA for a given day. Each regression is run on a sample of CSAs that either had an order issued on the day of interest, never had an order issued, or had an order issued later than April 6. As a result, each ω1 is estimated relative to the set of CSAs that never had orders or had orders after April 6. The regressions include CSA fixed effects µi and date fixed effects δt . CSAs are weighted by population in the regression. Robust standard errors are used for the line of best fit. 43 Appendix Figure A6: Effect of Stay-at-Home Orders, Reopening Panel A: Effect on Mobility 0.40 0.20 Coefficient Estimate 0.00 -0.20 -0.40 -21 -14 -7 0 7 14 21 Days Relative to Order Panel B: Effect on Consumer Spending 0.40 0.20 Coefficient Estimate 0.00 -0.20 -0.40 -21 -14 -7 0 7 14 21 Days Relative to Order Panel C: Effect on Employment 0.40 0.20 Coefficient Estimate 0.00 -0.20 -0.40 -21 -14 -7 0 7 14 21 Days Relative to Order Note: Figure plots estimated treatment effects ωk from the removal of stay-at-home orders on different outcomes, using the event-study specification outlined in equation (1) at the CSA-day level using data from March 1, 2020 to July 31, 2020. Panel A shows the effect on mobility, using the log of total POI visits in SafeGraph data. Panel B shows the effect on consumer spending, using the log of total spending in Facteus’ debit card sample. Panel C shows the effect on employment, using the log number of individuals with positive work hours from the Homebase sample. All regressions include CSA fixed effects µi and date fixed effects δt . CSAs are weighted by population in the regression. Standard errors are clustered at the CSA level irrespective of order timing. 44 Appendix Figure A7: Effect of Stay-at-Home Orders on Alternative Economic Outcomes Panel A: Log Number of Debit Transactions (Facteus) 0.40 0.20 Coefficient Estimate 0.00 -0.20 -0.40 -21 -14 -7 0 7 14 21 Days Relative to Order Panel B: Log Work Hours (Homebase) 0.40 0.20 Coefficient Estimate 0.00 -0.20 -0.40 -21 -14 -7 0 7 14 21 Days Relative to Order Panel C: Log Total Wages (Homebase) 0.40 0.20 Coefficient Estimate 0.00 -0.20 -0.40 -21 -14 -7 0 7 14 21 Days Relative to Order Note: Figure plots estimated treatment effects ωk from the event-study specification outlined in equation (1). Relative to Figure 4, we use alternative economic outcome measures. Panel A includes as the dependent variable the log number of debit transactions in Facteus’ debit card sample; Panel B uses the log number of work hours from Homebase; and Panel C gives the log total wages from Homebase for a given home CSA and day. All plots include CSA fixed effects µi and date fixed effects δt . CSAs are weighted by population in the regression. Standard errors are clustered at the CSA level irrespective of order timing. 45 Appendix Figure A8: Simulations Panel A: Preferred estimator τ=0 τ=-.1 0.30 0.30 0.20 0.20 Coefficient Estimate Coefficient Estimate 0.10 0.10 0.00 0.00 -0.10 -0.10 -0.20 -0.20 -0.30 -0.30 -21 -14 -7 0 7 14 21 -21 -14 -7 0 7 14 21 Days Relative to Order Days Relative to Order Panel B: Preferred estimator but not controlling for log(Iit ) τ=0 τ=-.1 0.30 Coefficient Estimate 0.30 Coefficient Estimate 0.20 0.20 0.10 0.10 0.00 0.00 -0.10 -0.10 -0.20 -0.30 -0.20 -0.30 -21 -14 -7 0 7 14 21 -21 -14 -7 0 7 14 21 Days Relative to Order Days Relative to Order Panel C: Log cases event study with linear time trends (Dave et al. 2020) τ=0 τ=-.1 0.30 0.30 0.20 0.20 Coefficient Estimate Coefficient Estimate 0.10 0.10 0.00 0.00 -0.10 -0.10 -0.20 -0.20 -0.30 -0.30 -21 -14 -7 0 7 14 21 -21 -14 -7 0 7 14 21 Days Relative to Order Days Relative to Order Note: Figure plots estimated treatment effects ωk from the event-study specification outlined in equation (11) using the data simulated from an SIRD model. The first column uses data simulated from an SIRD model where the true treatment effect of the stay-at-home order is τ = 0. The second column uses data simulated from an SIRD model where the true treatment effect of the stay-at-home order is τ = −.1. Panel A our preferred estimator. Panel B is the preferred estimator, but does not control for log(Iit ). Panel C is Dave et al. (2020) estimator that uses log cases on the left-hand side and controls for geography-specific linear time trends. Geographies are weighted by population in the regression. Standard errors are clustered at the geography level. 46 Appendix Figure A9: Simulations with Alternative Specifications Panel A: Preferred estimator but adding geography FEs τ=0 τ=-.1 0.30 0.30 0.20 0.20 Coefficient Estimate Coefficient Estimate 0.10 0.10 0.00 0.00 -0.10 -0.10 -0.20 -0.20 -0.30 -0.30 -21 -14 -7 0 7 14 21 -21 -14 -7 0 7 14 21 Days Relative to Order Days Relative to Order Panel B: Preferred estimator but setting γ at half its true value τ=0 τ=-.1 0.30 0.30 0.20 0.20 Coefficient Estimate 0.10 Coefficient Estimate 0.10 0.00 0.00 -0.10 -0.10 -0.20 -0.20 -0.30 -0.30 -21 -14 -7 0 7 14 21 -21 -14 -7 0 7 14 21 Days Relative to Order Days Relative to Order Panel C: Preferred estimator but setting γ at twice its true value τ=0 τ=-.1 0.30 0.30 0.20 0.20 Coefficient Estimate Coefficient Estimate 0.10 0.10 0.00 0.00 -0.10 -0.10 -0.20 -0.20 -0.30 -0.30 -21 -14 -7 0 7 14 21 -21 -14 -7 0 7 14 21 Days Relative to Order Days Relative to Order Note: Figure plots estimated treatment effects ωk from the event-study specification outlined in equation (11) using the data simulated from an SIRD model. The first column uses data simulated from an SIRD model where the true treatment effect of the stay-at-home order is τ = 0. The second column uses data simulated from an SIRD model where the true treatment effect of the stay-at-home order is τ = −.1. Panel A is the preferred estimator, but adds geography fixed effects. Panel B is the preferred estimator, but sets γ to half its true value. Panel C is the preferred estimator, but sets γ to twice its true value. Geographies are weighted by population in the regression. Standard errors are clustered at the geography level. 47 Appendix Figure A10: Effect of Stay-at-Home Orders on Contact Rate, All γ Values Panel A: γ = 0 Panel B: γ = 1/12 1.00 1.00 0.75 0.75 0.50 0.50 Coefficient Estimate Coefficient Estimate 0.25 0.25 0.00 0.00 -0.25 -0.25 -0.50 -0.50 -0.75 -0.75 -1.00 -1.00 -14 -7 0 7 14 21 -14 -7 0 7 14 21 Days Relative to Order Days Relative to Order Panel C: γ = 1/9 Panel D: γ = 1/6 1.00 1.00 0.75 0.75 0.50 0.50 Coefficient Estimate Coefficient Estimate 0.25 0.25 0.00 0.00 -0.25 -0.25 -0.50 -0.50 -0.75 -0.75 -1.00 -1.00 -14 -7 0 7 14 21 -14 -7 0 7 14 21 Days Relative to Order Days Relative to Order Panel E: γ = 1/3 Panel F: γ = 1 1.00 1.00 0.75 0.75 0.50 0.50 Coefficient Estimate Coefficient Estimate 0.25 0.25 0.00 0.00 -0.25 -0.25 -0.50 -0.50 -0.75 -0.75 -1.00 -1.00 -14 -7 0 7 14 21 -14 -7 0 7 14 21 Days Relative to Order Days Relative to Order Note: Figure plots estimated treatment effects ωk from the event-study specification outlined in equation (15) using the log of new cases in a state for a given day as in Panel A of Figure 5. Each panel uses a different value of γ. CSAs are weighted by population in the regression. Standard errors are clustered at the CSA level irrespective of order timing. 48 Appendix Figure A11: Dave et al. (2020) Estimators for Effect of Stay-at-Home Orders on COVID Cases Panel A: 7-day Preperiod as in Dave et al. (2020) 2.00 1.50 1.00 Coefficient Estimate 0.50 0.00 -0.50 -1.00 -1.50 -2.00 -21 -14 -7 0 7 14 21 Days Relative to Order Panel B: 14-day Preperiod 2.00 1.50 1.00 Coefficient Estimate 0.50 0.00 -0.50 -1.00 -1.50 -2.00 -21 -14 -7 0 7 14 21 Days Relative to Order Panel C: 21-day Preperiod 2.00 1.50 1.00 Coefficient Estimate 0.50 0.00 -0.50 -1.00 -1.50 -2.00 -21 -14 -7 0 7 14 21 Days Relative to Order Note: Figure plots estimated treatment effects ωk from the event-study specification outlined in equation (16) using the log of cases in a state for a given day and including state-specific linear trends. Panel A restricts the preperiod to 7 days. Panels B and C are the same as Panel A, except they use a 14- and 21-day preperiod. States are not balanced across the event window. States are weighted by population in the regression. Data is restricted to dates on or before April 20, 2020. Standard errors are clustered at the state level. 49 Appendix Figure A12: Effect of Stay-at-Home Orders on Change in Log New Deaths Panel A: γ = 0 1.00 0.75 Coefficient Estimate 0.50 0.25 0.00 -0.25 -0.50 -0.75 -1.00 -1.25 -1.50 -1.75 -2.00 -14 -7 0 7 14 21 Days Relative to Order Panel B: γ = 1/6 1.00 0.75 0.50 Coefficient Estimate 0.25 0.00 -0.25 -0.50 -0.75 -1.00 -1.25 -1.50 -1.75 -2.00 -14 -7 0 7 14 21 Days Relative to Order Note: Figure plots estimated treatment effects ωk from the event-study specification outlined in equation (15) using the log of new deaths in a CSA for a given day. Panel A only includes date fixed effects δt and sets γ = 0 which implies log(Iit ) = log(Cit ). Panel B is the same as Panel A, except that it sets γ = 1/6. CSAs are weighted by population in the regression. Standard errors are clustered at the CSA level irrespective of order timing. 50 Appendix Figure A13: Determinants of Variation in Log Contact Rates, Not Controlling for Mobility Panel A: Univariate Regression of θˆi on Covariates Log Pop. Log Pop. Density Frac. Urban Share 4-year Degree Share Hispanic Share Race - Other Share Race - Asian Share Race - White Share Race - Black Share Age <18 Share Age ≥65 Republican Vote Share Log International Flights Share Commute by Car Avg. Summer Temp. Avg. Winter Temp. Log Tests -.75 -.5 -.25 0 .25 .5 .75 Standardized Coefficient Panel B: Controlling for Log Population Log Pop. Log Pop. Density Frac. Urban Share 4-year Degree Share Hispanic Share Race - Other Share Race - Asian Share Race - White Share Race - Black Share Age <18 Share Age ≥65 Republican Vote Share Log International Flights Share Commute by Car Avg. Summer Temp. Avg. Winter Temp. Log Tests -.75 -.5 -.25 0 .25 .5 .75 Standardized Coefficient Note: Figure plots the coefficients of regressing the CSA log contact rate fixed effect estimates θˆi from equation (14) on CSA-level determinants, except that the change in social distancing is not subtracted prior to computing the fixed effects. The θˆi and all covariates have been standardized to have a mean 0 and a standard deviation of 1. Panel A plots the standardized coefficients and 95 percent confidence intervals from univariate regressions. Panel B repeats Panel A but the regressions also control for the log of population. Population weights are not used. Robust standard errors are used to compute the confidence intervals. 51 Appendix Table A1: Sources of Non-pharmaceutical Interventions Stay-at-home Business closures Unweighted Weighted Unweighted Weighted Inherited from State 0.898 0.464 0.923 0.629 NYT 0.895 0.638 0.000 0.000 Keystone Strategy 0.016 0.078 0.949 0.822 Crowdsourced 0.038 0.216 0.033 0.139 Hikma Health 0.018 0.057 0.016 0.038 Manual Entry 0.034 0.012 0.000 0.000 Note: Table summarizes the source of county stay-at-home and business closure policies. We report shares of county policies both unweighted and weighted by county population. The first row indiciates the share of county policies that are inheritied from the state; that is, counties did not enact the corresponding policy before the state took action. The remaing columns indicate the share of county policies coming from each of the our sources. The manual entry source is reserved for corrections to state policies which we hand checked. We only had to recode the Tennessee state policy. 52 Appendix Table A2: Decomposing Changes in Distancing, Economic, and Health Outcomes Panel A: Stay-at-Home Orders (1) (2) (3) k = 1 k = 20 Pre-Trend Total ∆ Policy-Induced ∆ POI Visits -0.672 -0.109 -0.165 -0.102 (0.008) (0.026) (0.028) Homebase Wages -0.590 -0.092 -0.197 -0.039 (0.013) (0.047) (0.049) Homebase Employment -0.592 -0.095 -0.206 -0.067 (0.012) (0.051) (0.053) Facteus Debit Transactions 0.048 -0.055 -0.071 -0.023 (0.007) (0.012) (0.014) Facteus Total Spending 0.284 -0.071 -0.034 0.006 (0.009) (0.020) (0.024) Panel B: Business Closure Orders (1) (2) (3) k = 1 k = 20 Pre-Trend Total ∆ Policy-Induced ∆ POI Visits -0.665 -0.060 -0.102 -0.060 (0.011) (0.031) (0.033) Homebase Wages -0.577 -0.105 -0.273 -0.353 (0.023) (0.093) (0.096) Homebase Employment -0.584 -0.093 -0.203 -0.262 (0.017) (0.068) (0.069) Facteus Debit Transactions 0.056 -0.017 -0.016 -0.006 (0.007) (0.021) (0.023) Facteus Total Spending 0.302 -0.012 0.017 -0.012 (0.010) (0.026) (0.029) Note: Table reports the total and policy-induced changes in various outcomes as outlined in Section 5.1 using alter- native estimators of the treatment effect. In Panel A, we consider the policy-induced changes of stay-at-home orders. In Panel B, we consider the policy-induced changes of business closure orders. For k = 1 and k = 20, we use the treatment effects ωk with corresponding value k. The ‘Pre-Trend’ estimator use the trend in estimates in the two weeks leading up to treatment to adjust the treatment effect ωk for k = 20. 53 Appendix Table A3: Variance Decomposition for Differences in Log Contact Rates Cross-CSA Variance of Log Contact Rate 1.514 Share of variance explained by: Social Distancing 0.008 Policy 0.000 Timing of Virus 0.001 Observed Covariates 0.264 Population 0.182 Climate 0.000 Transport 0.000 Race 0.032 Partisanship 0.031 College Degrees 0.000 Age Demographics 0.000 Note: Table reports the cross-CSA variance of the average log contact rate log(βit ) between March 15 and April 30, 2020 in the first row. We calculate the cross-CSA variance of each explanatory variable and report the share of the log contact rate variance accounted for by the variation in each set of explanatory variable using the estimated coefficients from our lasso model in Section 5.2. 54