key: cord-0997149-4lgy9te8 authors: Sears, J.; Villas-Boas, J. M.; Villas-Boas, V.; Villas-Boas, S. B. title: Are we #stayinghome to Flatten the Curve? date: 2020-05-26 journal: nan DOI: 10.1101/2020.05.23.20111211 sha: 52e3038903ef839e0bf0638bce3f40459aaf1aba doc_id: 997149 cord_uid: 4lgy9te8 The recent spread of COVID-19 across the U.S. led to concerted efforts by states to ``flatten the curve" through the adoption of stay-at-home mandates that encourage individuals to reduce travel and maintain social distance and indeed using data on travel activity we find that residents start reducing mobility early in most states. Combining data on changes in travel activity with COVID-19 health outcomes and variation in state policy adoption, we characterize the direct impact of stay-at-home mandates on mobility and social distancing and link these behavioral changes to health benefits. We find evidence of dramatic declines in mobility nationwide prior to the adoption of statewide mandates. Despite these early reductions, we find that statewide stay-at-home policies induced "mandate effects" of between 4.1 and 5.9 percentage point declines relative to pre-COVID-19 levels for the first four states to introduce such policies. These effects persist when considering all states' mandates and alternate estimation strategies that account for states' differences in travel behavior prior to policy adoption. Using previous changes in mobility, we find significant effects on current mortality, with 1% reductions in visits to non-essential businesses weeks prior being associated with 9.2 fewer deaths per 100 million per day, corresponding with over 74,000 lives saved nationwide and resulting economic benefits between $249-$745 billion for observed behavioral changes in March and April. Observed reductions in mobility indeed contribute to flattening the curve and reduce the strain on the medical system during those two months. Our findings provide evidence that statewide stay-at-home ordinances induce additional social distancing, and ultimately attenuate the negative health consequences of COVID-19, revealing themselves as important policy tools in the fight against pandemic. Further, substantial reductions in mobility prior to state-level policies convey important policy implications. Since December 2019, the novel coronavirus SARS-CoV-2 (COVID- 19) has spread rapidly around the world and in the U.S., prompting dramatic policy responses. Local, state, and national governments around the world face an extensive set of policy instruments with which to fight the pandemic and limit the virus' impact on their constituents. As many regions have exhibited exponential growth in coronavirus cases [26] , policymakers are increasingly implementing aggressive stay-at-home mandates to reduce transmission through human interaction and "flatten the curve" [45] [21] . As of March 31, the U.S. had the highest number of confirmed cases (more than 67% more than the next country) with at least one resident of every state affected [64] . Improving our understanding of how existing stay-at-home policies reduce travel activity and ultimately mitigate negative health consequences of the pandemic will help local and state policy makers determine the optimal policies for helping "flatten the curve" and quell the spread of COVID-19. To investigate this, we combine data on human mobility with state policy variation and health outcomes, allowing us to determine the reductions in distance traveled, visits to non-essential businesses, and human en-2 counters, and ultimately relate these to changes in hospitalizations and deaths directly attributable to mobility changes and stay-at-home mandates. While the benefits of non-pharmaceutical interventions (NPI), such as quarantining infected households, closing schools, and banning social events or large gatherings to reduce infection rates has largely been informed by mathematical models [35] , some anecdotal and historical evidence supports their efficacy. In California's San Francisco Bay Area, the first area of the country to implement stay-at-home mandates, doctors reported "fewer cases than expected" after two weeks of social distancing [39] . Analysis of internet-connected thermometers suggest that new fever rates on March 23 were below those at the start of the month, while state hospitalization rates showed a commensurate decline in growth rates [44] . Washington state officials reported similar reductions in COVID-19 transmission as a result of the state's containment strategies [9] . Exploration of death rates and NPI rollout in 17 U.S. cities during the 1918 influenza pandemic support these claims, finding that implementation of multiple social distancing practices intended to reduce infectious contacts between persons early in the outbreak led to 50% lower peak death rates and flatter epidemic curves relative to cities that did not implement such policies [35] . Gaining insight into the effectiveness of these stay-at-home mandates is critical for understanding the benefit of making the considerable economic sacrifices required to enact such policies. Even before mandates limited economic activity, GDP forecasts suggested an economic contraction in the U.S. five times greater than previous predictions [42] . Concerns over these costs prompted comments from the executive branch regarding relaxation of restrictions and allowing non-essential businesses to reopen [52] , prompting opposition from public health experts [31, 43] and economists [13, 36] . 3 Recent simulations provide further insight into the benefits of social distancing. While epidemiological models of the U.K. and U.S. suggest that techniques for mitigating exposure of those most at risk may drastically reduce peak load on the healthcare system and cut COVID-19 deaths by half, such techniques on their own might not be enough to prevent the healthcare system from being overwhelmed. Some argue that, in this case, a combination of social distancing, self-quarantine of infected, and suspension of schools would need to be maintained until a vaccine is available to prevent rebound [28] . Other experts call for widespread testing coupled with digital contact tracing as a means to reduce viral spread while minimizing harmful social and economic side-effects [30] . Simulations based on a moderate mitigation policy (comprised of 7-day isolation following any symptoms, a 14-day quarantine for the household, and social distancing for all citizens over age 70) implemented in late March find that such policies reduce potential U.S. deaths by 1.76 million deaths [34] . Given that this simulated policy is less stringent and maintained for a shorter duration than many of the policies currently observed, the actual benefits (either directly from reduced COVID-19 deaths or indirectly due to decreased transmission of other illnesses) from existing stay-at-home mandates could be substantially larger. This paper contributes to the existing literature by looking first at mobility patterns during the pandemic across states and time and second by providing the first empirical evidence of stay-at-home policies' effectiveness. These mandates combine closures of non-essential businesses with instructions for all residents to remain at home except for the purchase of necessities (i.e. groceries or medicine), with the goal of limiting "unnecessary person-to-person contact" [48] and to "mitigate the impact of COVID-19" [15] . We examine changes in travel behavior in response to these so-4 cial distancing policies due to the pandemic across the entire United States, estimate the portion of these reductions attributable to early state stay-at-home mandates, and correlate reduced travel behavior with changes in health outcomes weeks later. To estimate the changes in travel activity and social distancing since the spread of COVID-19 in the United States, we use data on changes in average distance traveled, visits to non-essential businesses, and unique human encounters per square kilometer by day and by state [63] relative to pre-COVID-19 baseline levels. Through data visualization and descriptive event studies, we show that tremendous nationwide reductions in travel activity levels occurred prior to statewide mandates, suggesting residents were already responding to local policies and perceived risks. By the time the average adopter has implemented its statewide mandate, average travel distances had already fallen by 38 percentage points, the human encounter rate by 76 percentage points, and non-essential visits by 52 percentage points, providing evidence of extensive social distancing occurring even before statewide orders requiring such behavior. We then estimate econometric models that isolate the effect of statewide mandates by comparing differences before and after mandate implementation and between early-adopting and control states. Identification of the stay-at-home policy effect originates from residual variation in changes to mobility measures relative to a state specific flexible trend, a day-to-day flexible national trend, and between mandate and non-mandate states. Using this panel fixed effects control structure, we test whether states' stay-at-home policies induce significant changes in mobility and human encounters by day in the United States once the mandate is implemented, relative to the change in non-mandate states. After presenting results from the difference-in-differences model, we employ the 5 health outcomes, controlling for state-specific trends in pandemic trajectories over tiem, and also for day-to-day changes common to all states and state-specific factors affecting health outcomes for all states, while also distinguishing between early mandate and all the mandate states. We find evidence that reduced travel does ultimately affect health outcomes, with reduced daily COVID-19 deaths of 9.2 per 100 million (0.092 per million) per day associated with a one percentage point reduction in past non-essential visits. Calculations of the resulting economic benefits suggest savings between $249 and $745 billion due to avoiding over 74,000 deaths from COVID-19 during the months of March and April, thus flattening the curve. We also find evidence of a relationship between reduced travel distance and COVID-19 mortality in early adoption states, suggesting economic benefits of $23.1-$99.1 billion and providing evidence that earlier implementation of non-pharmaceutical interventions may have increased the effectiveness of mobility reductions in reducing the spread of the pandemic. To our knowledge, ours is the first paper investigating mobility during the COVID-19 pandemic and providing evidence of reduced travel activity and social distancing and of health benefits associated with improved social distancing and reduced travel activity resulting from stay-at-home mandates and pre mandate mobility declines. We contribute to the overall understanding of the direct health benefits of current COVID-19 policies and provide evidence that these policies are having the intended effect of reducing social interactions and are correlated with reductions in negative health consequences from the current pandemic. Our findings that there are substantial reductions in mobility prior to state-level policies convey important policy implications. 7 . CC-BY-NC-ND 4.0 International license It is made available under a is the author/funder, who has granted medRxiv a license to display the preprint in perpetuity. (which was not certified by peer review) We obtain travel activity and social distancing data from the analytics company Unacast [63] . To understand how well different communities are social distancing, Unacast uses cellular location data for 15-17 million identifiers per day to construct three measures of behavior in response to COVID-19 policies [60] . Each measure is aggregated to the state by day level and is defined as the daily percentage point change relative to that weekday's average for the pre-COVID-19 period of the four weeks prior to March 8. While all data is published directly to their Social Distancing Dashboard in the form of figures and maps [60] , we obtained the balanced panel of state by day observations for the period of February 24 through April 29, 2020 directly from Unacast. Unacast receives location data from mobile devices through authorized applications, Wi-Fi or Bluetooth connections, and A-GPS positions. Obtained information includes the location of the device at a given point in time (latitude, longitude, and elevation) along with the mobile device make, model, and operating system, the corresponding application gathering the data, GPS accuracy value, and the direction and rate of travel. Each state-day observation we use is calculated using position information. The three measures we use together paint a comprehensive picture of behavior changes in response to state stay-at-home mandates. See the Data Appendix for more details on the data collection process, the equations used to construct each measure, and along with discussion on sample composition and potential biases or measurement errors. The first measure we use is the change in average distance traveled (ȦDT ), which 8 . CC-BY-NC-ND 4.0 International license It is made available under a is the author/funder, who has granted medRxiv a license to display the preprint in perpetuity. (which was not certified by peer review) captures changes in both the number of trips and the length of trips taken outside the home relative to the pre COVID-19 baseline period. Reductions in ADT following mandate implementation would reflect compliance on average with states' guidance to work from and stay at home except for essential activities. A value ofȦDT it = 0 indicates that the average distance traveled for individuals in state i on date t was identical to the pre-COVID-19 distance for that day of the week. A value of −7 conveys that, on average, devices assigned to the state traveled an average distance 7 percentage points shorter than during the pre-COVID-19 baseline. This approach allows us to account for differences in travel potential by day of week, making sure our comparison accurately reflects the average conditions for that day of the week prior to behavior and policy changes due to COVID-19. The second measure is the change in visits to non-essential businesses, defined as Non Essential Visits (Ṅ EV ). To the extent that non-essential businesses are closed following stay-at-home mandates, we expect to see reductions in the number of trips residents take to these types of retail or service businesses. Our utilized measure of the change in visits to non-essential businesses (Ṅ EV ) offers a similar comparison targeted at travel to the types of businesses most heavily impacted by stay-at-home mandates. Businesses likely to be deemed "non-essential" include department stores, spas and salons, fitness facilities, event spaces, and many others; non-essential businesses are defined according to group definitions in both the Unacast SDK and the OpenStreetMaps POI's to improve accuracy (see the data appendix for a table with the complete list of included business types). The metricṄ EV is constructed similarly toȦDT , replacing the average distance traveled per day with the average visitations to non-essential businesses and the baseline is again constructed as the average for a 9 given weekday in the pre-COVID-19 period for a given state. A value ofṄ EV it = 2 indicates a two percentage point increase in visitations to non-essential businesses relative to baseline norms for that weekday in a given state. Finally, we use changes in the rate of unique human encounters (ĖN C) as a measure of social distancing. Following [50] , (ĖN C) is calculated as the rate of unique human encounters per square kilometer, and is initially normalized relative to the national median over the four weeks prior to March 8. We further adjust the rate of encounters as the change relative to the state's mean change from the national average for the period February 24 to March 8 to match measurement of the other activity variables. 1 An encounter rate equal to that of the state baseline rate results in a value of EN C it = 0, while a value of EN C it = −12 indicates a 12 percentage point reduction in the encounter rate for state i on date t relative to the states' pre-COVID-19 level. In Table 1 we provide summary statistics for each of the three Unacast data measures by column, with rows organized into three panels. Each panel reports the averages, first and third quartiles, and medians for each mobility measure along with the count of observations during the week.The first panel corresponds to the last week in February, February 24-29, the first week for which data are available. The middle panel is for the month of March, and the bottom panel is for the month of April up to April 29th, 2020. In the top panel for the end of February, we see that average distance traveled was larger than pre-COVID-19 baseline levels by 2.49 percentage points. In column 2, we see that non-essential visits were 0.71 percentage points lower than the pre-COVID-19 baseline, with the rate of human encounters 2.8 percentage points higher in column 3. To denote periods before or after a state implemented a "stay at home order," we obtain the date each statewide policy was issued [45] for all fifty states and the District of Columbia. We define our early adopters as the first four states to implement a stay-at-home mandate: California, Illinois, New Jersey, and New York. The second group are the 39 late adoption states, and then the 8 remaining states that never implement statewide mandates: Arkansas, Iowa, Nebraska, North Dakota, Oklahoma, South Dakota, Utah, and Wyoming. The observed stay-at-home mandates all consist of a mix of specific non-pharmaceutical interventions; each observed policy closes or places considerable limits on non-essential businesses and requires residents to stay at home except for essential activities. Essential services include grocery stores, gas stations, pharmacies, banks, laundry services, and business essential to government function [16] . Throughout this paper we refer to all mandates that implement this combination of policies as a "stay-at-home mandate." While we focus our attention on statewide stay-at-home policies, many county and local policies had already been implemented and were already affecting individuallevel mobility around the country. Six San Francisco Bay Area counties required residents to stay-at-home beginning March 17, two days prior to the statewide mandate [55] . By mid-March, schools of all levels had begun closing their doors and transitioning to online instruction. On March 9, Stanford University moved classes online "to the extent possible," with Harvard and many other institutions swiftly following suit [38] . Further, business leaders including Google, Microsoft, Twitter, Facebook, and Amazon transitioned some or all of their employees to working remotely well before statewide mandates entered into effect [7] . As a result, any behavioral response to 13 . CC-BY-NC-ND 4.0 International license It is made available under a is the author/funder, who has granted medRxiv a license to display the preprint in perpetuity. (which was not certified by peer review) statewide stay-at-home mandates represents only a partial response to the suite of the actions and policies undertaken to combat the spread of COVID-19. Our estimated "mandate effects" that follow therefore capture the behavioral responses specific to statewide stay-at-home mandates and underestimate the effect of all combined policies. If local, county, and business policies had already incentivized residents to stay at home, then we would expect minimal response to later statewide mandates which would be reflected in weak small magnitude estimates in our models. Whatever impact our empirical methods are able to pick up reflects mobility responses in addition to those already realized for existing policies. We obtain information on hospitalizations and deaths due to COVID-19 by state from the COVID Tracking Project (CVT) [22] for the period of February 24 to May 2, 2020. CVT obtains data on positive and negative tests, deaths, hospitalizations, and the counts of patients currently in intensive care units and on ventilators. Outcome data are obtained directly from the respective public health authorities, supplemented with additions from press conferences or trusted news sources. As the bulk of data is obtained directly from state public health bodies, CVT represents one of the most transparent and up-to-date source of COVID-19 mortality and morbidity data. We scale the change in hospitalizations and deaths by state population in 100 millions. We obtain population data by state from the 2010 U.S. Decennial Census [61] . While all states report both the change and running total of deaths, reporting of hospitalizations is less consistent and often incomplete. Appendix Tables ***REF and REF*** summarize the data quality and coverage for deaths and hospitalizations across 14 . CC-BY-NC-ND 4.0 International license It is made available under a is the author/funder, who has granted medRxiv a license to display the preprint in perpetuity. (which was not certified by peer review) The copyright holder for this preprint this version posted May 26, 2020. . https://doi.org/10.1101/2020.05.23.20111211 doi: medRxiv preprint all states and Washington D.C. for states reporting and not reporting hospitalization data, respectively. As of May 2, 37 states report at least two days of hospitalization data while 13 states and Washington D.C. report no hospitalization data. Missing states include three of the first four early adopters: California, Illinois, and New Jersey. While states consistently report between 30 and 60 days of death data as both daily changes and running totals, hospitalization data is much more sparse and reported in different ways by different states. Alaska and Connecticut report hospitalization as both the daily change and running total, while the remaining 35 states only report the cumulative number of hospitalization by date. Hospitalization data coverage ranges from a minimum of 2 days (Connecticut) to a maximum of 42 days (Colorado, Florida, Massachusetts, New York, North Dakota, Ohio, and Oklahoma). As we utilize the daily change per 100 million residents as outcomes of interest in our main analyses, we convert all hospitalization data provided as sums only to the daily change before dividing by 100 million population. Health outcome summary statistics are provided in Table 2 . Table 2 CC-BY-NC-ND 4.0 International license It is made available under a is the author/funder, who has granted medRxiv a license to display the preprint in perpetuity. (which was not certified by peer review) The copyright holder for this preprint this version posted May 26, 2020. . https://doi.org/10.1101/2020.05.23.20111211 doi: medRxiv preprint deaths, with the average death rate for the period roughly 337 deaths per 100 million per day, with average hospitalization rates near 1080 per 100 million per day. Mortality and morbidity data obtained from CVT correlate strongly with other sources of COVID-19 health data. We chose CVT as our main source of health outcome data as they were found to balance transparency with coverage and stood as the most complete source of hospitalization data. We find evidence that the CVT measure of COVID-19 mortality correlates strongly with comparable measures obtained from other sources -see the Data Appendix for tables correlating CVT, the New York 16 . CC-BY-NC-ND 4.0 International license It is made available under a is the author/funder, who has granted medRxiv a license to display the preprint in perpetuity. (which was not certified by peer review) The copyright holder for this preprint this version posted May 26, 2020. . https://doi.org/10.1101/2020.05.23.20111211 doi: medRxiv preprint Times, and Johns Hopkins' death rates. This provides evidence for the insensitivity of our health findings to our choice of data source. While the measures of mortality and morbidity we employ represent the most upto-date data available, they are still preliminary and likely represent underestimates of the true impacts of COVID-19. Widespread lack of access to testing, especially in rural areas and early on in the U.S. outbreak, means many deaths (especially at-home deaths) due to respiratory issues caused by COVID-19 may have gone uncounted [14] . As more information becomes known, state health authorities are likely to update their reported counts. As CVT actively updates their data and we pull data directly from CVT each day, the numbers used in this paper accurately reflect mortality and morbidity information as is currently known at the time of writing. The true public health impact of COVID-19 will likely not be known for years to come as reporting protocol is improved and prior deaths are verified. To investigate how travel activity and social distancing behavior evolved day-to-day during the COVID-19 period, we begin by estimating an event study regression for each mobility measure: Here the change in mobility measureẎ is expressed as a function of a constant and a set of 49 indicator variables, equal to one in state s on the date k days since the state's 17 . CC-BY-NC-ND 4.0 International license It is made available under a is the author/funder, who has granted medRxiv a license to display the preprint in perpetuity. (which was not certified by peer review) The copyright holder for this preprint this version posted May 26, 2020. . https://doi.org/10.1101/2020.05.23.20111211 doi: medRxiv preprint first reported case and equal to zero otherwise. The coefficient β −1 is normalized to zero, such that all estimated coefficientsβ k measures the difference in the predicted change in mobility outcome Y relative to the day prior to a state's first case. We report estimates from Eq 1 using event study figures, allowing us to understand how behavior changes in a state are correlated with spread of COVID-19 within that state. As no additional controls are included, these figures merely report differences in conditional means and provide evidence of substantial changes in mobility patterns prior to states' implementation of stay-at-home mandates. To determine the effect of statewide stay-at-home mandates on travel activity, we begin by estimating the following model: Here the outcomeẎ sd denotes the change in a given measure of travel activity . CC-BY-NC-ND 4.0 International license It is made available under a is the author/funder, who has granted medRxiv a license to display the preprint in perpetuity. (which was not certified by peer review) The copyright holder for this preprint this version posted May 26, 2020. . https://doi.org/10.1101/2020.05.23.20111211 doi: medRxiv preprint daily changes in nationwide total deaths/hospitalizations). In our preferred specification we also include state-specific cubic time trends, 3 0 γ js t j = γ 0s +γ 1s t+γ 2s t 2 +γ 3s t 3 , allowing the effect of time elapsed since February 24 to affect each state differently in a flexible fashion. ε is an idiosyncratic error comprised of unobserved determinants of changes in travel activity that are not controlled for by the variables specified in the linear Eq 2. The coefficient β measures the difference in the change in average daily travel activity for states that implement the stay-at-home mandate relative to the change in activity in states that have yet to or never implement such policies, after controlling for state and time-varying factors that also correlate with changes in daily activity. In this wayβ provides an estimate of the average treatment effect for treated states (ATT). We estimate the model in Eq 2 using a daily state-level panel data set on changes in average travel activity by state and day. This empirical approach allows us to identify the relationship between stay-athome mandates and daily changes in each of the three measures while also explicitly controlling for other confounding factors that are specific to each state or date. The share of local population previously working from home or employed in specific industries are controlled for with η, while day-to-day changes in activity common to all states -motivated by new information on the virus' spread and nationwide media coverage or federal appeals to social distancing -are controlled for through δ. We include state-specific cubic trends, 3 j=0 γ js t j = γ 0s + γ 1s t + γ 2s t 2 + γ 3s t 3 , allowing the effect of time elapsed since late February to flexibly affect travel behavior in state s. 3 The mandate effect β is identified under the assumption that, after controlling for the state-specific trends, common day-to-day trends, and time-invariant state character- All empirical results that follow are obtained through unweighted ordinary least squares (OLS). We choose to report results for unweighted linear regression as we prefer the potential loss in efficiency from using heteroskedasticity-robust standard error procedures to the implications of a misspecified form of variance with weighted least squares (by imposing variance proportional to state population). Implicitly OLS would assign even weight to each state regardless of population in a two-by-two differencein-differences estimand with uniform adoption timing. However, weights become less straightforward in the panel setting with staggered adoption timing; applying population weights in this setting will apply additional weighting schemes on top of exist-20 . CC-BY-NC-ND 4.0 International license It is made available under a is the author/funder, who has granted medRxiv a license to display the preprint in perpetuity. (which was not certified by peer review) The copyright holder for this preprint this version posted May 26, 2020. . https://doi.org/10.1101/2020.05.23.20111211 doi: medRxiv preprint ing weights due to variation in policy timing and group comparisons [32] . Further, weighting would not allow us to recover a consistent estimator for the population average effect in the presence of over or under-sampling of particular groups in our state averages [57] . Given that group membership is determined by location of residence, individual observations within a state are likely not independent and the population of a state may not substantively influence the variance of the population residual. In this case, weighting by population could reduce efficiency of the estimator and bias standard errors [24] . Given an error-components model for single period individual error terms of the form ij = c i + u ij the variance for a particular state's average error becomes where σ 2 c represents a group-specific variance and σ 2 u the idiosyncratic error, with J i the number of devices observed in group i. Given that each observation in our sample is an aggregation of travel activity conducted by millions of individuals, the second term will be negligible in comparison to the group-level variance component. In this case, introducing population weights would exacerbate heteroskedasticity and lead to lower precision than in OLS [24] . Here, the number of individuals contained in each states average is very large and we have no evidence that these sampled individuals are more or less likely to respond to SAH policies than the average american. Given the lack of evidence of endogenous sampling, use of population weights in our chosen 21 . CC-BY-NC-ND 4.0 International license It is made available under a is the author/funder, who has granted medRxiv a license to display the preprint in perpetuity. The copyright holder for this preprint this version posted May 26, 2020. . control structure would not offer a consistency gain [57] . To allow more transparent understanding as to how our overall ATT estimate is obtained, we explore the role of policy timing and group comparisons in informing the DD estimator weights in the Appendix ***REF***. Further, our later use of partially pooled synthetic control weights in a weighted event study designs in decomposes the ATT by time elapsed since mandate adoption while controlling for endogenous treatment timing. A primary concern for violation of the difference-in-differences identifying assumption rests on the endogeneity of mandate adoption timing. If states that chose to adopt mandates early did so due to larger initial case counts or earlier realizations of a first death from COVID-19, then travel behavior by that states' residents may have already been trending differently than that for residents of states that had not yet adopted a mandate. To account for differences between early and late adoption states, we conduct analysis using the weighted event study approach of [10] that extends the synthetic control method to the staggered adoption panel setting and the event study framework that nests within the fixed effects approach employed earlier. The synthetic control method (SCM), developed by [1] , creates a "synthetic" control group for a single treated unit using weights to balance the treatment and synthetic control groups on pre-treatment outcomes. As SCM does not require as strong a parallel trend assumption as difference-in-differences (now requiring that an appropriate counterfactual can be obtained using the convex hull of untreated units), it quickly became a preferred tool of applied researchers. While this offered a clear advantage for identifying a valid counterfactual, it was not immediately clear how to extend the 22 . CC-BY-NC-ND 4.0 International license It is made available under a is the author/funder, who has granted medRxiv a license to display the preprint in perpetuity. The copyright holder for this preprint this version posted May 26, 2020. . https://doi.org/10.1101/2020.05.23.20111211 doi: medRxiv preprint approach into panel data settings with multiple treated units receiving treatment potentially at different points in time. Partially pooled SCM integrates the two most common ad-hoc approaches (applying synthetic control separately to each treated unit before taking an average across treated units, and estimating weights to fit the average pre-treatment outcome for all treated units) in a manner that simultaneously minimizes error arising from both the singleunit fits and the pooled fit [10] . While the approach does not guarantee perfect balance of both unit-specific and overall pre-treatment outcomes, it offers a way to minimize the sources of bias associated with each choice on its own. Let Y it (1) be the potential outcome for unit i in period t after having received the treatment, and let Y it (0) be the potential outcome for a unit in the absence of treatment (i.e. that has yet to receive treatment or never receives the treatment). In our setting, 43 units eventually adopt a stay-at-home mandate (42 states and Washington D.C.), and are denoted by W i = 1. W i = 0 for the eight states that never adopt a mandate. We can then express the observed outcome for the units that adopt a mandate at time In this framework an estimate for the average treatment effect on the treated (ATT) is given by where k indicates the "event time" elapsed relative to the treatment time T j , given 23 . CC-BY-NC-ND 4.0 International license It is made available under a is the author/funder, who has granted medRxiv a license to display the preprint in perpetuity. The copyright holder for this preprint this version posted May 26, 2020. . https://doi.org/10.1101/2020.05.23.20111211 doi: medRxiv preprint (1) is observed for all treated units after mandate adoption, and following [10] the unobserved potential outcomeŶ j,T j +k (0) is obtained through a modified SCM approach using the available donor pool at time T j + k (units that have yet to receive treatment or never receive treatment). For treated units j 1 , ..., j J , the N-vector SCM weightsτ j are the solution to the partially pooled SCM optimization problem: In contrast to [1] , weights are based solely on lagged outcomes with the potential f (τ ij ) to promote uniformity. 4 q pool is the mean square error for the average of the pre-treatment periods across all J treated units when running SCM separately for each unit, and q sep the equivalent object when SCM is applied to the "pooled" average of all treated units. ν ∈ [0, 1] is the hyperparameter determining the weight given to each SCM approach; a value of ν = 0 corresponds to separate SCM weights while ν = 1 yields weights derived from the pooled SCM approach. In this way the partially pooled SCM weights trade off imbalance resulting from state-specific matches with the pooled imbalance; see [10] for additional discussion of the balance possibility frontier. The partially pooled SCM approach can obtain a causal estimate of the average treatment effect on the treated (ATT) under two key assumptions [8] . First, we assume that a treated unit's potential outcomes prior to receiving treatment are equal to the control unit's potential outcomes: Y it (s) = Y it (0) for t < s. This assumption serves as a generalization of SUTVA, ruling out interference across states in our setting [54] . 4 We set λ = 0 for our estimation as we have a sufficiently large donor pool to obtain pre-treatment balance 24 . CC-BY-NC-ND 4.0 International license It is made available under a is the author/funder, who has granted medRxiv a license to display the preprint in perpetuity. The copyright holder for this preprint this version posted May 26, 2020. . https://doi.org/10.1101/2020.05.23.20111211 doi: medRxiv preprint Second, we must assume that, for a given unit with W i = 1, the potential outcomes following treatment are identical to the observed treated potential outcome: Y it (s) = Y it (1) for any 0 < s ≤ t . This assumption imposes stability of the treatment effect over time within a given unit while still allowing {Y it (0), Y it (1)} to vary across units. To correct for imperfect pre-treatment balance in partially pooled SCM, we augment the partially pooled SCM estimator with a fixed effects outcome model and estimate weighted event studies. Synthetic controls are constructed based on the balance of residualized pre-treatment outcomes; in this way the approach builds upon recent research on doubly-robust estimators with an extension to the staggered adoption setting [2, 5, 6, 10, 20] . The weighted event study obtains the counterfactual for treated unit j, k periods after adopting a mandate aŝ Whereτ * ij are partially pooled SCM weights obtained using residualized outcomes andm ijk is obtained as the uniformly-weighted average of pre-period outcomes, equivalent to augmentation with unit fixed effects. This approach yields a unit-specific ATT estimate k periods post-adoption as 25 . CC-BY-NC-ND 4.0 International license It is made available under a is the author/funder, who has granted medRxiv a license to display the preprint in perpetuity. The copyright holder for this preprint this version posted May 26, 2020. . This approach builds upon the robustness properties of the intercept-shifted or demeaned SCM estimators in a way that allows for staggered adoption [25, 29] . AT T aug jk can be thought of as a doubly-weighted difference in differences estimator, wherein the change in the treatment unit is obtained as the difference between the treatment unit's outcome in period k and its pre-period average, and the change in the control group is the average for equivalent changes for all donor units, weighted by partially . Standard errors are obtained using a jackknife approach [6] . Finally, we consider a distributed lag model specification to empirically test whether changes in mobility weeks prior have an effect on current health outcomes from COVID-19. Across models we control for day-to-day changes common to all states and statespecific factors affecting health outcomes, state-specific trends affecting health outcomes, and distinguish between mandate and non-mandate states. We model daily new COVID 19 deaths and hospitalizations per 100 million residents by state as Where H sd is the daily health outcome reported for state s on date d, andṀ OB s,−k is the lagged change in the chosen mobility measure (one of average distance traveled, ADT , non-essential visitsṄ EV , or human encountersĖN C). k ∈ {1, 2, 3} so that 26 . CC-BY-NC-ND 4.0 International license It is made available under a is the author/funder, who has granted medRxiv a license to display the preprint in perpetuity. The copyright holder for this preprint this version posted May 26, 2020. . Ȧ DT s,−1 ,ȦDT s,−2 andȦDT s,−3 are the changes in the average distance traveled in the previous week, 2 weeks, and 3 weeks, respectively. In each of the empirical analyses, the coefficient α is a constant, 3 0 γ js t j are state specific cubic trends controlling for time-variant state characteristics that affect health outcomes, and δ d date fixed effects controlling for common time shocks measured relative to the first period. The disturbance ε sd are unobserved determinants of health outcomes that vary over time within a given state that cannot be explained by the flexible trend. For changes in average distance traveled, in Eq 6, the coefficient onȦDT s,−3 captures the estimated effects of reducing activity three weeks prior. Inclusion of additional lags for one and two weeks prior allows us to estimate a lagged long term impact of reducing activity; in this case, the long term impact of changes in activity is given by the sum of the three lagged variable coefficients of the lagged changes in average distance traveled one, two and three weeks prior. Similar interpretation applies to the models for the other two lagged measures. We estimate the equation for all states, and then separately for early mandate and for all mandate states. Across the United States, COVID-19 upended daily routines. As a result of layoffs, revised work-from-home guidelines, school closures, family needs, and state policies, travel behavior has changed dramatically in the U.S. over the last two months. Figure 1 plots over time the changes in average distance traveled (ȦDT ), visits to non-essential businesses (Ṅ EV ), and the unique human encounter rate (ĖN C) per day for all U.S. states, measured as the percent change relative to typical pre-COVID-19 levels. The solid line plots the average for the first four states to implement mandatory stay-at-27 . CC-BY-NC-ND 4.0 International license It is made available under a is the author/funder, who has granted medRxiv a license to display the preprint in perpetuity. The copyright holder for this preprint this version posted May 26, 2020. Travel behavior in late February and through the first week of March looks largely typical for distances traveled and visits to non-essential businesses, with small fluctuations relative to baseline activity levels for all states. The change in the human encounter rate exhibits much greater variation throughout the week, increasing over the course of the work week before falling considerably over the weekend. Despite this greater within-week variation, the average human encounter rate for all states finishes the work week of March 2-6 above baseline levels. Beginning the week of March 9, residents across the country began deviating from typical travel patterns. By Wednesday March 11, residents of all states had begun reducing their distances traveled, trips to non-essential businesses, and encounters with others relative to pre-COVID-19 norms. Initially, changes to mobility patterns in early-adoption states is largely indistinguishable from those for other states; by March 15, residents across all three groups had reduced travel distance by 8 to 13 percentage points, unique human encounters by 28 to 29 percentage points, and visits to nonessential visits by 12 to 17 percentage points. By March 18, before the first statewide mandate went into effect, these declines had grown dramatically in magnitude. The decline in travel distances grew in magnitude 5 Colorado, Connecticut, Delaware, Hawaii, Idaho, Indiana, Louisiana, Michigan, New Mexico, Ohio, Oregon, Vermont, Washington, West Virginia, and Wisconsin all implement similar stay-at-home mandates between March 23 and March 26. Massachusetts adopted a stay-at-home advisory, recommending but not requiring that residents stay home. . CC-BY-NC-ND 4.0 International license It is made available under a is the author/funder, who has granted medRxiv a license to display the preprint in perpetuity. The copyright holder for this preprint this version posted May 26, 2020. Figure 1 : Each series represents the change in each day's mobility measure relative to pre-COVID-19 levels for the given groups of states. The solid line corresponds to the average change for the four states that implemented stay-at-home mandates by end-of-day March 22 (California, Illinois, New Jersey, and New York). The dotted line plots the average for the 39 states that adopted statewide mandates at later points, while the dashed line represents the average for the eight states that never adopted a statewide mandate. The first panel plots changes in average distance traveled, the second changes in unique human encounters per square kilometer, and the third changes in visits to non-essential businesses. The gray bars designate weekend days while the vertical line indicates March 19, the date the first state policy was implemented in California. to between 12 and 23 percentage points, and between 34 to 49 percentage points fewer non-essential visits. Unique human encounters had already fallen between 61 and 71 percentage points relative to pre-COVID-19, a dramatic indicator of extensive social distancing occurring even before statewide orders requiring such behavior. By the time many state implemented their policies in the coming weeks, travel 29 . CC-BY-NC-ND 4.0 International license It is made available under a is the author/funder, who has granted medRxiv a license to display the preprint in perpetuity. The copyright holder for this preprint this version posted May 26, 2020. . https://doi.org/10.1101/2020.05.23.20111211 doi: medRxiv preprint behavior and social interactions had already largely bottomed out. While gaps begin appearing in mobility patterns for residents of early adoption, later adopters, and never adopter states at this time, these gaps and weekly patterns remain remarkably consistent through mid-April. To investigate how changes in travel activity evolved in response to a state's COVID-19 outbreak, we next present estimates from the event study model in Eq 1 in Figure 2 . Each panel plots the point estimates and 95% confidence interval for the effect of being k days away from the state's first reported COVID-19 case. As the effect for the baseline period k = −1 is normalized to zero, all coefficient estimates are interpreted as the difference in mobility changes relative to the day before a state's first case. . CC-BY-NC-ND 4.0 International license It is made available under a is the author/funder, who has granted medRxiv a license to display the preprint in perpetuity. The copyright holder for this preprint this version posted May 26, 2020. . CC-BY-NC-ND 4.0 International license It is made available under a is the author/funder, who has granted medRxiv a license to display the preprint in perpetuity. Across our three mobility measures, we observed a decline nearly monotonic in time elapsed since a state's first case. While travel activity is generally slightly higher or indistinguishable from baseline levels for the few pre-case periods in our sample, activity begins a nearly linear decline after the first case. This roughly linear trend continues for distances traveled for the next thirty days, before bottoming out around a 40 percentage point reduction. The unique human encounter rate displays a similar pattern, with its decline slowing after 2 weeks' time before reaching a stable level around an 80 percentage point reduction. Changes in non-essential visits follow suite, declining rapidly over the first two weeks of outbreak before fluctuating between a 50 to 60 percentage point reduction. Additionally, we see that dramatic reductions in travel behavior occurred prior to statewide SAH mandates. By the time the average adopter has implemented its statewide mandate, average travel distances had already fallen by 38 percentage points, the human encounter rate by 76 percentage points, and non-essential visits by 52 percentage points. While small reductions in travel activity measures occur more than 21 days after a first COVID-19 case, they are generally not distinguishable from effects on the 21st day. For periods 22 or more days after the first case, only 5 days for travel distance, 2 days for human encounters, and 7 days for non-essential visits are statistically 32 . CC-BY-NC-ND 4.0 International license It is made available under a is the author/funder, who has granted medRxiv a license to display the preprint in perpetuity. The copyright holder for this preprint this version posted May 26, 2020. . https://doi.org/10.1101/2020.05.23.20111211 doi: medRxiv preprint distinguishable at the 95% level from comparable changes on the 21st day. While Figures 1 and 2 provide preliminary evidence that residents across the country have drastically reduced travel activity and engaged in social distancing in response to COVID-19 and that residents of mandate states differentially modified their travel behavior, it is difficult to visually isolate the share of the difference attributable to states' stay-at-home mandates from time trends and characteristics of state residents and policies. To investigate the role of stay-at-home mandates for early adopter states further, we next present results of empirical specifications designed to isolate the effect of stay-at-home policies on changes in travel activity and social distancing for the first four states to adopt them. In the empirical regression approaches that follow in this section, we attempt to isolate the effect of states' stay-at-home mandates on travel behavior. We start by focusing our attention on estimating the average treatment effect on the treated (ATT) for early adopter states (CA, IL, NJ, and NY). Given that, unlike in many other locations, residents of these states had yet to reach their minimum travel levels before their states' mandates came into effect. Restricting our attention to policy variation in these four states initially will help shed light on whether the greater propensity of residents in these states to further reduce travel in the post-mandate period plays a role in the size of any "mandate effect" we obtain. After discussing results for early adopters, we expand our focus to all states that adopt stay-at-home mandates. We begin by presenting the results of the linear fixed effects model from Eq 2 in Table 3 for changes in average distances traveled before presenting results for preferred 33 . CC-BY-NC-ND 4.0 International license It is made available under a is the author/funder, who has granted medRxiv a license to display the preprint in perpetuity. The copyright holder for this preprint this version posted May 26, 2020. . https://doi.org/10.1101/2020.05.23.20111211 doi: medRxiv preprint specifications across all three mobility outcomes in Table 4 . . CC-BY-NC-ND 4.0 International license It is made available under a is the author/funder, who has granted medRxiv a license to display the preprint in perpetuity. The copyright holder for this preprint this version posted May 26, 2020. . https://doi.org/10.1101/2020.05.23.20111211 doi: medRxiv preprint (7) correspond to the staggered difference-in-differences estimator with various time controls. In column (2) we add state fixed effects, and in column (3) we further add an indicator for all days following implementation of the first state mandate on March 19 (Af ter 1st M andate) and dummy variables for each day of the week. In column (4) we add date fixed effects, which controls day-to-day changes common to all states, and estimate a -4.5 change due to early mandates. Columns (5) to (7) include state-specific trend controls: in column (5) we control for state-by-week fixed effects, in column (6) for state-specific cubic splines with knots on Feb 29, Mar 19, Apr 1, and Apr 15, and in column (7) we control for a state-specific cubic trend. When we add state-by-week fixed effects to day-of-week controls in column (5) we see that the estimated treatment effect of the early mandates increases in magnitude to -10.2 percentage points. Including state-specific flexible trends in columns (6) and (7) results in ATT estimates closer in magnitude to those of the two-way fixed effects estimator in column (4), with an estimate of -4.1 with either state-specific cubic splines or state-specific cubic trends. In column (6) and (7) we use the residual variation in average distance traveled that is not explained by state-specific time trends to estimate the treatment effects of the early stay at home mandates. We see that our estimates for the changes in average distances traveled stand as quite robust to considering state-specific time factors, which is the most conservative variation to use. Table 4 consolidates estimates for the effect of early stay-at-home mandates on travel activity and presents results across all three mobility measures. For each measure we present estimates from the two-way fixed effects specification and with statespecific cubic time trends. Columns (1) and (2) present results for changes in travel 35 . CC-BY-NC-ND 4.0 International license It is made available under a is the author/funder, who has granted medRxiv a license to display the preprint in perpetuity. The copyright holder for this preprint this version posted May 26, 2020. . https://doi.org/10.1101/2020.05.23.20111211 doi: medRxiv preprint activity from columns (4) and (7) in Table 3 , while columns (3) and (4) present results from corresponding models for changes in non-essential visits, with results for changes in human encounter rates in columns (5) and (6) . Across all columns and time control structures, we estimate large magnitude changes in travel activity due to early stay-at-home mandates. Looking at estimates for changes in visits to non-essential businesses, we observe treatment effect estimates of -6.1 and -5.2 percentage points for columns (3) and (4), respectively, with both statistically significant beyond the 1% level. That is, once a mandate is implemented, we estimate a 5.2 to 6.1 percentage point reduction in the change in average visits to non-essential businesses per day relative to control states. Given an average reduction of 59 percentage points across all states during the month of April, this corresponds to an additional 9 to 10% reduction in addition to prior reductions. Turning next to changes in human encounter rates in columns (5) and (6), we once again observe a relatively large response to stay-at-home mandates. We obtain ATT 36 . CC-BY-NC-ND 4.0 International license It is made available under a is the author/funder, who has granted medRxiv a license to display the preprint in perpetuity. The copyright holder for this preprint this version posted May 26, 2020. . https://doi.org/10.1101/2020.05.23.20111211 doi: medRxiv preprint estimates of −6.9 and −4.7 percentage points once a mandate is implemented, indicating that unique human encounters per square kilometer declined in response to early stay-at-home mandates. Once again the treatment effects are statistically significant beyond the 1% level. While individuals had reduced their daily encounter rates by 79 percentage points on average for the month of April, early mandates encouraged an additional 6-9% reduction. To understand whether later adopters attained reductions in travel activity akin to those observed for early adopters, we next present results of Eq 2 utilizing variation in mandate timing for all states that ever adopted a statewide stay-at-home mandate. We present the difference-in-differences results for all states's mandates in Table 5 . Using all adopting states provides much greater variation in treatment timing; in this way the ATT estimates will be identified both through comparisons of changes in treated units to changes in states that never adopted a mandate and through comparisons of 37 . CC-BY-NC-ND 4.0 International license It is made available under a is the author/funder, who has granted medRxiv a license to display the preprint in perpetuity. The copyright holder for this preprint this version posted May 26, 2020. . states that have adopted and have yet to adopt at a given point in time. Across all columns and time control structures, we find continued evidence of mandates' effects on travel behavior. ATT estimates in Table 5 are all statistically significant beyond the 1% level and appear similar to those found for the first four adopters, albeit with smaller magnitude changes when allowing for state-specific time trends. In column (1) under the two-way fixed effects control structure we see that, once a mandate is implemented, residents reduce their average distance traveled by an additional 5.5 percentage points relative to control states (states that never adopt and those that have yet to adopt. This point estimate is larger than the ATT estimate of −4.5 when restricting attention just to early mandates. When we add flexible state-specific trends in column (2), the ATT estimates decreases in magnitude to −2.8, below the −4.1 estimate for early mandates, but remains distinguishable from no effect. Changes in visits to non-essential businesses and human encounters display a similar pattern. Across all states that ever adopt a statewide mandate, we estimate a "mandate effect" of −5.2 and −4.5 for changes in non-essential visits without and with cubic state time trends, respectively. These estimates are within 0.7 − 0.9 of the comparable estimates for early adopters, suggesting that much of the mandate's impact remained even for mandates adopted much later in the pandemic. Turning to changes in human encounter rates, we similarly estimate a treatment effect of −4.6 percentage points per day with two-way fixed effects and −3.6 when including state-specific cubic time trends. These findings provide evidence that the effectiveness of states' mandates was not entirely dependent on early adoption. While estimated effects of stay-at-home mandates are slightly larger in magnitude than for early adopters than those adopted at 38 . CC-BY-NC-ND 4.0 International license It is made available under a is the author/funder, who has granted medRxiv a license to display the preprint in perpetuity. The copyright holder for this preprint this version posted May 26, 2020. . any point during the spread of pandemic, all ATT estimates are markedly different from zero. The larger magnitude effect for early mandates may simply be a product of individuals' propensity to reduce travel when the mandates came into effect. When California, Illinois, New Jersey, and New York adopted their mandates, travel activity across the country was still in decline. By the time many later adopters' policies entered into effect in late March or Early April, residents were already largely staying home and social distancing -either due to local mandates, loss of a job or work from home policies, or voluntary decisions to self-mitigate risk of infection. The fact that we are able to find evidence of additional reductions in travel activity for later mandates supports the effectiveness of these policies in achieving their states goals. Taken together, we find that people across the U.S. decreased their travel and rate of human encounters early in the pandemic, preempting statewide requirements. Moreover, we find that statewide stay-at-home mandates are related to significant reductions in all our measures of travel activity, with residents of early mandate states engaging in social distancing at greater rates than individuals not subject to such policies. This mandate effect persists when considering all statewide policies, suggesting that adoption early in a states' pandemic curve was not a necessity for inducing additional behavior modification. Distance traveled is positively linked to an increased number of social trips across all modes of transportation [62] , suggesting that the observed decreases likely reflect a decline in unique trips away from home as well. As travel activity is a main source of social interaction beyond one's immediate family [56] and travel to non-work locations increases the probability of co-location with others [59] , these reductions in distances traveled likely reflect commensurate decreases in physical interactions with 39 . CC-BY-NC-ND 4.0 International license It is made available under a is the author/funder, who has granted medRxiv a license to display the preprint in perpetuity. The copyright holder for this preprint this version posted May 26, 2020. . those outside of one's immediate family. Our estimates for changes in unique human encounters reflect these previous studies, providing evidence of further social distancing once states adopted a stay-at-home mandate. Further, these findings are not limited to the Unacast mobility measures; use of Google's COVID-19 Community Mobility Reports estimates similarly large and statistically significant effects of statewide mandates. 6 All this provides consistent, preliminary evidence that stay-athome mandates are having the intended effect of inducing greater social distancing than would occur otherwise, helping to reduce the opportunities for communication of COVID-19 within communities. A potential concern of the difference-in-differences estimator relates to the weighting of individual periods. Under staggered adoption, the estimated treatment effect can be expressed as a weighted average of all unique two-period by two-group differencein-difference estimators [32] . Weights are implicitly assigned to each timing cohort and unit, proportional to the variance of the treatment indicator in each period and the size of each cross-sectional group. A key implication of these weights is a favoring of units treated near the middle of the sample period, with non-convexity indicating a potential for negative weights ( [2, 12, 23] . Another consequence is that negative treatment effects could also be obtained even when the effect of stay-at-home mandates for all adopting states are positive [17] . To shed light on how the difference-in-differences ATT estimates presented earlier rely on these timing and group weights, we decompose the two-way fixed effects esti- 6 See the Appendix for the complete complementary google mobility analysis, replicating the same methodology controlling for state specific flexible trends, state, and day fixed effects. . CC-BY-NC-ND 4.0 International license It is made available under a is the author/funder, who has granted medRxiv a license to display the preprint in perpetuity. The copyright holder for this preprint this version posted May 26, 2020. . https://doi.org/10.1101/2020.05.23.20111211 doi: medRxiv preprint mates from column (4) of Tables 4 and 5 into their component two-by-two comparisons following [32] . We find that after decomposing the ATT for early adopters' mandates into its nine simple comparisons, over 99% of the weight falls on comparisons of treatment vs. control units (states that never adopt or adopt later). Of these comparisons, Illinois and New Jersey versus control states receives the majority of the ATT weight . CC-BY-NC-ND 4.0 International license It is made available under a is the author/funder, who has granted medRxiv a license to display the preprint in perpetuity. The copyright holder for this preprint this version posted May 26, 2020. . https://doi.org/10.1101/2020.05.23.20111211 doi: medRxiv preprint To address concerns regarding imbalances in changes to mobility patterns in the premandate period, we next present results from the weighted event study. As these estimates construct a counterfactual balanced on pre-treatment outcomes for each adopting state, the estimated ATT now more closely reflects the comparison of the postadoption oeriod for each state to an appropriate trend from the pool of donor units available at each point in time. We begin by presenting the weighting event study figures for the heuristic ν of [10] , equal to ν = q pool / √ q sep the ratio of the square roots of pooled to separate SCM imbalance. A larger ν trades off reductions in pooled imbalance for increases in separate state imbalances. We compare the results to an unweighted event study approach and discuss the evolution of mandate effects with time elapsed post-treatment. We next present overall mandate effect estimates across the space of ν. While an interior nu of 0.01 − 0.99 offers substantial imbalance reductions relative to the pooled or separate SCM cases, the optimal choice of ν is not immediately obvious. Estimating weighted event studies over the range of ν allow us to better understand how sensitive the overall ATT estimate is to the shift in weight from separate SCM for each state to a purely pooled SCM approach. is the author/funder, who has granted medRxiv a license to display the preprint in perpetuity. The copyright holder for this preprint this version posted May 26, 2020. . approach of the weighted event study necessarily imposes balance on changes in pretreatment outcomes. The typical event study (left panel) plots day-to-day ATT estimates averaged across all adopting states obtained from a two-way fixed effects control approach akin to columns (1), (3), and (5) in table 5 with a vector of dummy variables for being each of k ∈ {−44, 21} days relative to mandate adoption. The day prior to adoption (k = −1) is normalized to zero, such that all point estimates are interpreted as a differential change in a given travel outcome on the k th day since mandate adoption relative to the day immediately preceding adoption. 95% confidence intervals clustered at the state level are reported in the gray band. Estimates statistically distinguishable from zero in the post-period measure the treatment effect of stay-at-home mandates on mobility patterns, decomposed by day. Non-zero estimates in the pre-mandate period (k < 0) are evidence that the difference-in-differences parallel trends assumption is likely violated: residents of adopting states were already differentially modifying their travel behavior relative to residents of control states prior to any statewide mandates requiring such behavior. Typical event studies for all three travel activity show both an immediate, shortterm mandate effect and considerable differential trends in the pre-mandate periods. Looking first at changes in average distance traveled in Figure 3 , we observe a statistically significant treatment effect of −3 to −4 percentage points immediately following mandate adoption that persists for five days. An immediate drop of 5 − 6 percentage points is observed for non-essential visits and human encounter rates on the day following mandate adoption. While both effects remain distinguishable from zero for a longer period of time than for distance traveled, neither effect persists for more than 43 . CC-BY-NC-ND 4.0 International license It is made available under a is the author/funder, who has granted medRxiv a license to display the preprint in perpetuity. The copyright holder for this preprint this version posted May 26, 2020. Figure 3 : Standard and weighted event studies for changes in average distance traveled following state mandates. The standard event study (left panel) plots regression coefficients for dummy variables equal to one for being k days away from the first effective date of each statewide stay-at-home mandate, with 95% clustered standard errors represented in the gray band. A point estimate of -10 indicates a 10 percentage point greater decline in the average distance traveled per day for a state k days since mandate adoption relative to the day prior to mandate adoption (k = −1). The left panel plots equivalent point estimates and jackknife standard errors from a weighted event study, with partially pooled synthetic controls constructed to match treated units on residualized pre-treatment outcomes. two weeks following mandate adoption. All three panels display considerable differences in trends between treatment and control groups; travel activity levels in mandate states begin 20-25 percentage points lower than in control states. These trends follow roughly linear trends, and remain non-parallel for the entire pre-mandate period for both non-essential visits and the human encounter rate. Once differences in pre-trends are correctly internalized, a much clearer picture of stay-at-home mandates' effectiveness becomes visible. Results from the weighted event studies presented in the right panels of Figures 3, 4, and 5 show the considerable improvements in pre-treatment balance, with a total of three out of 129 pre-period estimates distinguishable from zero (in contrast to a combined 89 for the standard event studies). Further, we now observe persistence of the estimated mandate effects, with travel behavior falling discontinuously immediately after a mandate and per-44 . CC-BY-NC-ND 4.0 International license It is made available under a is the author/funder, who has granted medRxiv a license to display the preprint in perpetuity. The copyright holder for this preprint this version posted May 26, 2020. . https://doi.org/10.1101/2020.05.23.20111211 doi: medRxiv preprint The consistency of estimates between the difference-in-differences and weighted 7 See Appendix ***REF*** for overall ATT estimates across the entire space of ν. . CC-BY-NC-ND 4.0 International license It is made available under a is the author/funder, who has granted medRxiv a license to display the preprint in perpetuity. The copyright holder for this preprint this version posted May 26, 2020. While stay-at-home mandates reducing travel activity and promoting increased social distancing behavior provides evidence that individuals are listening to their states' 46 . CC-BY-NC-ND 4.0 International license It is made available under a is the author/funder, who has granted medRxiv a license to display the preprint in perpetuity. The copyright holder for this preprint this version posted May 26, 2020. . ordinances even after substantial earlier behavior modification, what matters from a public health perspective is the impact of these behavioral changes on the spread of and outcomes from COVID-19. Increased social distancing and reduced travel away from home and non-essential trips are mechanisms through which the transmission of COVID-19 can be reduced, and are main mechanisms affected by statewide stayat-home mandates. Merging the daily state-level changes in travel activity and social distancing [63] with the daily changes in COVID-19 deaths and hospitalizations per state [22] , we are able to provide early indications of whether the stay-at-home mandates are having their intended effects of mitigating the pandemic's health consequences. Prior to the implementation of stay-at-home policies we find no statistical evidence of differential trends for early-adopter states relative to the rest of the US for the period February 24 through March 8. Conducting a difference-in-means test for the two groups, we fail to reject the null hypothesis that the average change in distance traveled (t-statistic of -1.67) and deaths per million (t = 0.72) each day are different for CA, IL, NJ, and NY relative to other states. 8 To investigate the time patterns of health outcomes we start by breaking up the average death rate by day separately for two groups of states: those that are mandate states and the eight states that are not. In Figure 6 we see that average death rates increase more for states that are not implementing mandates than for those states that do and that the patterns for hospitalization rates are noisier, as show in the bottom panel of this figure. 8 We do not conduct a comparable test for hospitalization, ICR and ventilator rates due to the lack of consistent data and possibly inconsistent reporting across states in the weeks prior to March 19. We also have data for the share of COVID-19 positive tests by day and by state but we reject the null hypothesis of no difference in means for the share of positive tests (t = 4.11), which we take as further evidence that testing volumes and protocols differ extensively from state to state. . CC-BY-NC-ND 4.0 International license It is made available under a is the author/funder, who has granted medRxiv a license to display the preprint in perpetuity. The copyright holder for this preprint this version posted May 26, 2020. Looking at the time patterns for states that experience the largest reductions in mobility and distinguish from the average death rates for the states that experience the lowest mobility reductions (lower than the median drop), as measured by daily changes in non essential visits, we show in Figure 7 that the increase in death rates is steeper for those states that have the smallest reductions in mobility while once again the hospitalization rate patterns are noisy. 9 While Figures 6 and 7 provide preliminary evidence of variation over time in death rates across states that are correlated with stay-at-home mandate adoption decisions 9 The pattern is similar for other break downs along average distance traveled and encounter rates as shown in the Appendix. . CC-BY-NC-ND 4.0 International license It is made available under a is the author/funder, who has granted medRxiv a license to display the preprint in perpetuity. The copyright holder for this preprint this version posted May 26, 2020. is the author/funder, who has granted medRxiv a license to display the preprint in perpetuity. The copyright holder for this preprint this version posted May 26, 2020. . comes, we next present results from statistical analyses designed to isolate the variation in mortality and morbidity associated with changes in travel activity. In particular, we present results of estimating Eq 6 to test whether changes in distance traveled, non-essential visits, and human encounter rates one, two, and three weeks prior have an effect on current health outcomes. We specify daily changes in deaths and hospitalizations per 100 million population as our dependent variables. Eq 6 controls for state-specific flexible time trends, day-to-day changes common to all states, and state-specific factors affecting health outcomes. The inclusion of lagged effects for one and two weeks prior allows us to measure any cumulative long-term impact of reducing activity during the prior three weeks. Finding evidence of any such cumulative long-term effects of lagged mobility changes on current deaths would provide preliminary evidence that these behavioral changes may ultimately play a valuable role in flattening the curve and reducing the severity of COVID-19 pandemic. In addition to estimating Eq 6 using nationwide data, we also run analyses limiting the sample to the first four early adopters. We observe a greater post-mandate period for these states, during which the nature of non-essential visits and human encounters would likely differ from that in states yet to adopt mandates. Residents of early adoption states would have more rapidly seen non-essential businesses adopt policies targeted at restricting foot traffic and improving sanitation. Similarly, the propensity for transmission from human encounters differs when wearing face coverings and maintaining at least six feet of distance from others. To the extent that we find a differential impact in early mandate states, this provides preliminary evidence that the suite of non-pharmaceutical interventions set in place for early stay-at-home mandates convey positive cumulative long-term health impacts. . CC-BY-NC-ND 4.0 International license It is made available under a is the author/funder, who has granted medRxiv a license to display the preprint in perpetuity. The copyright holder for this preprint this version posted May 26, 2020. . * p < 0.10, ** p < 0.05, ** p < 0.01. Robust standard errors reported in parentheses. These models estimate the relationship between changes in average distances traveled per day and COVID-19 health outcomes. The dependent variables measure the number of new daily deaths or hospitalizations per 100 million population in a given state. Columns (1) and (2) . CC-BY-NC-ND 4.0 International license It is made available under a is the author/funder, who has granted medRxiv a license to display the preprint in perpetuity. The copyright holder for this preprint this version posted May 26, 2020. . https://doi.org/10.1101/2020.05.23.20111211 doi: medRxiv preprint The results from the estimation of Eq 6 for changes in average distance traveled per day are presented in Table 6 . Given that we use three weeks' lagged data on changes in distance traveled, our first day in the estimation sample is March 16th. The day-to-day fixed effects therefore measure changes in the health outcomes common to all states relative to March 16th. We also include state-specific cubic trends to account for variations in outbreak development over time unique to each state. Column (1) The first row reports the coefficient on the change in average distance traveled one week prior, followed by the standard error, then the coefficient for two weeks prior, followed by three weeks prior. We cannot reject the null that none of these coefficients are different from zero. The long-term impact, which corresponds to the cumulative effect of −0.779+2.67+2.76 = 4.65 over all lagged weeks is positive but not statistically significant, with an F statistic of 4.7 for the null hypothesis of the sum being equal to zero (p-value of 0.11). We find no evidence of a significant estimated long-term impacts for hospitalizations in column (2) . Finally focusing at column (3), changes in 52 . CC-BY-NC-ND 4.0 International license It is made available under a is the author/funder, who has granted medRxiv a license to display the preprint in perpetuity. The copyright holder for this preprint this version posted May 26, 2020. . https://doi.org/10.1101/2020.05.23.20111211 doi: medRxiv preprint average distance traveled three weeks prior in early mandate states is associated with significant effects on current death rates. The long-term impact, which corresponds to the cumulative effect of 4.63 + 6.35 + 59.38 = 68.36 fewer daily deaths per 100 million, is a positive and significant effect with an F statistic of 4.6 (p-value of 0.04). Focusing now on changes in visits to non-essential businesses (Ṅ EV ), we present the results from the estimation of Eq 6 in Table 7 . The regressions are comparable to those presented in Table 6 , and measure the effect of changes in N EV on deaths or hospitalizations per 100 million residents. As in Table 6 all columns include state and date fixed effects, and state-specific cubic trends. Once again we find evidence of long-term health benefits following reductions in 53 . CC-BY-NC-ND 4.0 International license It is made available under a is the author/funder, who has granted medRxiv a license to display the preprint in perpetuity. The copyright holder for this preprint this version posted May 26, 2020. . https://doi.org/10.1101/2020.05.23.20111211 doi: medRxiv preprint non-essential travel for all states. A one percentage point reduction inṄ EV three weeks prior is associated with 6.6 fewer daily deaths per 100 million across all states in column (1) and 24 fewer deaths per 100 million in early mandate states (column 3). We estimate no significant lagged effects on hospitalization rates in column (2) . Looking at column (1), the estimated cumulative effect for daily deaths of −0.068+2.64+6.59 = 9.2 over lagged weeks for the entire U.S. is positive. This long-run effect displays strong statistical significance, with an F statistic of 6.6 for the null hypothesis of the sum being equal to zero (p-value of 0.01). The estimated long-term impact for early mandates states in column (3) is not statistically significant (p value of 0.27). Finally, we present evidence of changes in social distancing behavior on COVID-19 health outcomes in Table 8 . While point estimates of the long-term cumulative effects of prior reductions in human encounters on COVID-19 death rates are positive for all states and for only early adopters, none exhibit statistical significance. Once again we find no statistical evidence of changes in hospitalization rates. . CC-BY-NC-ND 4.0 International license It is made available under a is the author/funder, who has granted medRxiv a license to display the preprint in perpetuity. The copyright holder for this preprint this version posted May 26, 2020. . . CC-BY-NC-ND 4.0 International license It is made available under a is the author/funder, who has granted medRxiv a license to display the preprint in perpetuity. The copyright holder for this preprint this version posted May 26, 2020. . https://doi.org/10.1101/2020.05.23.20111211 doi: medRxiv preprint The estimated significant long-term impact of past changes in non-essential visits of 9.2 fewer deaths per 100 million is robust to including other controls, such as lagged changes in other mobility measures. In particular, we estimate a significant long-term impact of non-essential visits, controlling for changes in lagged encounter rates and also state specific trends, and find that a drop of non-essential visits of one percentage point three weeks prior has a long term impact of reducing daily death rates by . CC-BY-NC-ND 4.0 International license It is made available under a is the author/funder, who has granted medRxiv a license to display the preprint in perpetuity. The copyright holder for this preprint this version posted May 26, 2020. . https://doi.org/10.1101/2020.05.23.20111211 doi: medRxiv preprint Our estimates are an average of the effects of behavioral changes that occurred early in the COVID-19 pandemic as well as after states began implementing health policies. We estimate significant cumulative long-term effects of lagged mobility on current deaths, which provides preliminary evidence that the behavioral changes of reductions in mobility do contribute to flattening the health outcome curves weeks later. Specifically, we estimate that a one percent reduction in non-essential travel three weeks earlier has a significant long-term correlation of reducing deaths by 9.2 per 100 million each day. Given that residents across the U.S. averaged a decline of 40 percentage points in non-essential visits relative to baseline levels in the months of March and April, this would correspond to an estimated 360 (40 × 9) fewer daily deaths per 100 million residents. Using the estimated mandate-induced changes in non-essential visits of -4 percentage points from the weighted event study analyses, this is 10% of the overall reductions during this period and corresponds to a decline of 36 deaths per day due to mandate-induced behavior changes. We estimate a differential impact in mandate states which provides preliminary evidence that mandate policies convey long-term health impacts. Further, we estimate a differential impact in mandate states, providing preliminary evidence that stay-at-home mandates may convey positive cumulative long-term health impacts. Specifically, we estimate that a one percent reduction in average distance traveled three weeks earlier is significantly associated with 70 fewer deaths per 100 million per day. Given that on average residents across the U.S. CC-BY-NC-ND 4.0 International license It is made available under a is the author/funder, who has granted medRxiv a license to display the preprint in perpetuity. The copyright holder for this preprint this version posted May 26, 2020. . deaths per million. Given the estimated mandate effect of a 6 percentage point reduction in average distance traveled obtained from the weighted event studies, this implies that 20% of these overall declines in deaths are attributable to mandate-induced behavioral changes, or roughly 4 fewer daily deaths per million residents. When considering the extent of pre-mandate and mandate-induced behavior changes, there is evidence of considerable economic benefits across a range of value of statistical life (VSL) estimates. A value of $10 million corresponds to the United States Environmental Protection Agency's central VSL estimate, recommended for benefit calculation use "regardless of the age, income, or other population characteristics of the affected population" [27] . While this value may reasonably capture the average impact of air or water pollution on the population at large, it does not accurately reflect the demographics of those most affect by COVID-19: the elderly [19, 53] . To account for the greater mortality risk associated with older cohorts, we also present calculations using two alternate VSL estimates. First is the cohort-adjusted value utilized by the Council of Economic Advisers (CEA) for pandemic guidelines [18] , adjusted for current COVID-19 death rates. In their report for mitigating future pandemic from influenza, the estimates from the semi-logarithmic hedonic wage regression with compensating replacement rates approach of [3] and applies adjustments by age cohort to account for differences in pandemic mortality rates. Their approach yields a population-weighted average of $8.87 million in 2018 dollars, or $9.06 million in 2020. When adjusting this estimate for age cohort death rates for COVID-19, [58] obtain a revised estimate of $5.77 million per statistical life. This $5.77 million estimate more accurately reflects the conditions of pandemic in the United States. . CC-BY-NC-ND 4.0 International license It is made available under a is the author/funder, who has granted medRxiv a license to display the preprint in perpetuity. The copyright holder for this preprint this version posted May 26, 2020. Table 9 provides estimates of the economic benefits due to averted deaths from mandate-induced changes in travel activity in early adoption states. Using the EPA and adjusted CEA estimates give estimates that more closely reflect values used for federal policy guidance, while the life expectancy-adjusted approach of [58] provides a more targeted estimate than the utilized government guidelines that more closely reflects the economic costs associated with lives lost from COVID-19. To obtain an estimate of the economic benefit from stay-at-home mandate-induced travel activity changes in early adoption states, we multiply the 4 fewer daily deaths per million obtained earlier with estimates of the mandate-induced travel activity changes attained from the difference-in-differences and weighted event study approaches. Column (4) of Table 4 yielded a mandate ATT of a −4.1 percentage point change in av- . CC-BY-NC-ND 4.0 International license It is made available under a is the author/funder, who has granted medRxiv a license to display the preprint in perpetuity. The copyright holder for this preprint this version posted May 26, 2020. . 60 . CC-BY-NC-ND 4.0 International license It is made available under a is the author/funder, who has granted medRxiv a license to display the preprint in perpetuity. The copyright holder for this preprint this version posted May 26, 2020. A similar approach yields valuations of the benefits of travel reductions from all sources during the COVID-19 period in Table 10 . As seen in Figures 1 and 2 , residents across the country greatly reduced visits to non-essential businesses well before states implemented their mandates. Results from the health analyses in Table 7 found a 11 The −6 estimate is obtained from a model comparable to Figure 3 using only the first four adoption states as the treated group with ν = 0.49. See Appendix ***REF*** for a summary of overall ATT estimates for weighted event studies specific to early adoption states. . CC-BY-NC-ND 4.0 International license It is made available under a is the author/funder, who has granted medRxiv a license to display the preprint in perpetuity. . CC-BY-NC-ND 4.0 International license It is made available under a is the author/funder, who has granted medRxiv a license to display the preprint in perpetuity. (which was not certified by peer review) The copyright holder for this preprint this version posted May 26, 2020. . https://doi.org/10.1101/2020.05.23.20111211 doi: medRxiv preprint Temporarily closing non-essential businesses and mandating residents stay at home except for essential activity is the prime policy instrument currently employed by states to promote social distancing and slow the transmission of COVID-19. If effective, these policies will have reduced strain on the medical system and provided much-needed time for the development of pharmaceutical treatments that can reduce transmission rates and end the pandemic. If unsuccessful, states will have incurred large economic costs with few lives saved. Whether these mandates cause people to stay at home and engage in social distancing is a key requirement of a successful policy. Knowing whether such policies will have their intended effect is of increasing policy relevance as all but eight states eventually adopted such policies. Understanding if and how individuals reduce travel activity in response to stay-at-home mandates and maintain social distance is the primary empirical question we tackle in this paper. First, we find that by the time the average adopter has implemented its statewide mandate, residents had already reduced travel by considerable amounts relative to pre-COVID-19 levels. Average travel distances had already fallen by 38 percentage points, human encounter rates by 76 percentage points, and non-essential visits by 52 percentage points before the first statewide mandate came into effect, providing evidence of extensive social distancing occurring even before they were required by statewide orders. Second, we find evidence that adoption of state-level stay-at-home mandates induced further reductions in all three travel activity measures. The mandate effect persists not just for the early adoption states (where residents' travel activity had not yet stabilized at new, lower norms) but also for mandates adopted weeks later. For the 63 . CC-BY-NC-ND 4.0 International license It is made available under a is the author/funder, who has granted medRxiv a license to display the preprint in perpetuity. (which was not certified by peer review) The copyright holder for this preprint this version posted May 26, 2020. . https://doi.org/10.1101/2020.05.23.20111211 doi: medRxiv preprint early mandate states of California, Illinois, New Jersey, and New York, our staggered difference-in-differences models estimate a reduction in average distance traveled of 4.1 percentage points, a decline in visits to non-essential businesses of 5.2 percentage points, and a decrease in the rate of unique human encounters of 4.7 percentage points relative to pre-COVID-19 baselines. These effects remain present when considering all mandates implemented, albeit to a slightly smaller degree, with mandate ATT estimates of a −2.8 change in distance traveled, −4.5 change in non-essential visits, and a −3.6 change in unique human encounters. Estimated magnitudes remain highly comparable when directly accounting in differences in pre-mandate behavior for treatment and control states. Through the weighted event studies that construct control units to balance pre-treatment travel behavior net of state fixed effects, we find large, statistically significant drops immediately following mandate implementation that persist for the duration of the sample period. Resulting estimates of the overall mandate effects range between -7.29 and -6.47 for changes in average distance traveled, between -4.38 and -4.14 for non-essential visits, and between -5.87 and -4.98 for any mix of pooled and separate synthetic control weights. Our estimates suggest that, importantly, residents subject to stay-at-home mandates are on average responding as desired to curb the spread of COVID-19. Our empirical approaches isolate the mandate effect from other drivers of daily changes in travel activity levels, state-specific trends, and controls for a host of potential confounding factors that differ between states that adopted early policies relative to other states. In spite of these rigorous control approaches, we find persistent evidence of state mandates inducing further reductions in travel activity even after considerable earlier declines around the country. Further, our estimates are average treatment ef-64 . CC-BY-NC-ND 4.0 International license It is made available under a is the author/funder, who has granted medRxiv a license to display the preprint in perpetuity. (which was not certified by peer review) The copyright holder for this preprint this version posted May 26, 2020. . https://doi.org/10.1101/2020.05.23.20111211 doi: medRxiv preprint fects in response to statewide mandates only; given the extents of prior school closures, new work from home abilities, and county-level stay-at-home policies, our findings represent only a portion of the way individuals responded to COVID-19 policies and are a considerable lower bound on how individuals responded to all COVID-19 policies. Linking changes in travel activity and social distancing to health outcomes, we find evidence that these reductions help "flatten the curve" and reduce health consequences. We find that, on average, a one percentage point decrease in non-essential visits per day three weeks prior has a long-term average effect of reducing nationwide death rates by 0.92 fewer deaths per million per day. Converting these reductions in deaths to economic benefits, we find that the observed reduced travel activity nationwide during the months of March and April translate into savings of $249-$755 billion due to associated reductions in deaths. Further, we find evidence of differential declines in deaths from shorter distances traveled in the first four states to adopt statewide mandates. Residents of these state were subject to modified business policies and face covering requirements for greater periods of time; our findings provide preliminary evidence that the non-pharmaceutical interventions employed by statewide mandates helped further flatten these states' epidemic curves. The reductions in deaths from a month-long mandate in these states are associated with total savings between $23.1 and $99.1 billion. Our findings have important policy implications for the fight against COVID-19. First, individuals on average responded as intended to statewide mandates. Despite considerable prior reductions, residents heeded their states' requests and stayed at home. Second, the declines in economic activity directly attributable to statewide 65 . CC-BY-NC-ND 4.0 International license It is made available under a is the author/funder, who has granted medRxiv a license to display the preprint in perpetuity. (which was not certified by peer review) The copyright holder for this preprint this version posted May 26, 2020. . https://doi.org/10.1101/2020.05.23.20111211 doi: medRxiv preprint mandates may be much smaller than previously thought. As individuals around the country had already more than halved the quantity of trips taken to non-essential retail and service businesses, much of the lost business and resulting unemployment would have likely still occurred even if states had not adopted their stay-at-home policies. Further, as the mandate-induced reductions in visits to non-essential businesses amount to only one-tenth of the overall reductions since COVID-19, it is likely that loosening or removing statewide policies on their own will not be sufficient to induce mobility patterns to quickly return to pre-COVID-19 levels. Further policies will be needed to ensure that individuals can resume activity and return to local businesses in a manner that is safe. Our estimates do not take into account the benefits from avoided hospitalizations and other indirect health benefits from reduced travel activity and social distancing. As reductions in travel distance and increased social distance likely decrease exposure to other potentially deadly illnesses, this is likely an underestimation of the overall health benefit of these policies. Further, the patterns in under-reporting and undercounting of COVID-19 deaths provide further evidence that we likely underestimate the direct benefits of these policies. Future identification of additional COVID-19 deaths may prove difficult, as many death certificates list only the immediate cause of death and fail to report underlying diseases -likely understating the presence of COVID-19 [40] . Further, procedures for counting COVID-19 deaths may be correlated with adoption of stay-at-home mandates. If adoption of a state-level ordinance indicates additional preparedness on the part of the adopting state, then states that were slower to (or had yet to) pass stay-at-home mandates may also have been slower to properly attribute deaths to COVID-19, resulting in our estimated effects being under-66 . CC-BY-NC-ND 4.0 International license It is made available under a is the author/funder, who has granted medRxiv a license to display the preprint in perpetuity. (which was not certified by peer review) The copyright holder for this preprint this version posted May 26, 2020. . https://doi.org/10.1101/2020.05.23.20111211 doi: medRxiv preprint statements of the true effect. Given the challenges to proper identification of COVID-19 deaths we may not know the true death count for years, or ever. As a result it may not ever be possible to determine the exact loss of life due to COVID-19, and accordingly we heed caution in interpreting our result as capturing a de-facto relationship. We support continued efforts to obtain accurate counts of the mortality and morbidity consequences from COVID-19 to help ensure future research can provide sufficient policy guidance in the case of future pandemics. While this paper sets out to understand an important and timely question and provides benefit estimates to help policymakers evaluate tradeoffs and weigh the costs and benefits of extending and relaxing such policies, there are avenues for future research that could be explored. First, whether these policies result in a true flattening of the epidemic curve or merely postpone illness is an avenue that deserves additional attention. Particularly as states weigh the difficult decisions of reopening business as usual, it is necessary to understand how caseloads and health consequences may rebound. Second, future work should also consider within-state policy variation and the relationship between local and national policies. Knowing whether county-level mandates that preceded statewide policies conveyed additional benefits will help improve our understanding of the full set of policy tools available to combat future pandemics. Further, the economic forces and psychological incentives behind compliance with stay-at-home mandates are complex, and additional work is needed that can characterize the mechanisms behind the policy effects we observe. . CC-BY-NC-ND 4.0 International license It is made available under a is the author/funder, who has granted medRxiv a license to display the preprint in perpetuity. 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