Back to school: The effect of school visits during COVID-19 on COVID-19 outcomes

Abstract

The effects of school closures on COVID-19 transmission remain unclear, even after the conclusion of the national Public Health Emergency. We use healthcare claims data from 130 million household-week observations linked to smartphone mobility data to measure the effects of changes in county-level visits to schools on COVID-19 outcomes. We use a triple-differences approach that leverages within-county differences in exposure between families with and without school-age children and find modest impacts. We find increases in COVID-19 infection rates, with larger differences in low-income and higher COVID-19 prevalence counties.

1. Introduction

Early in the COVID-19 pandemic, school closures were seen as a mitigation and containment strategy to prevent the spread of the virus (Donohue and Miller, 2020). By April 2020, all 50 states closed elementary and secondary public schools for the remainder of the academic year to slow COVID-19 transmission (Kaufman et al., 2021), although many schools eventually reopened. There were two primary rationales for the enactment of these closures. First, the risk of COVID-19 infection to children was not known during the initial stage of the pandemic. Second, children were assumed to be important vectors for the spread of COVID-19 (Christakis et al., 2020). Both factors were critical, given that between 33.9 million and 44.2 million adults with risk factors for severe COVID-19 had direct or within-household connections to schools (Selden et al., 2020).

However, the extent to which school reopenings contributed to COVID-19 transmission among both children and adults remains unclear. As discussed below, the social proximity of in-person schools creates opportunities for disease spread. At the same time, schools and households may respond to increased risks of school transmission by reducing other sources of COVID-19 risk (Arrow, 1951; Peltzman, 1975; Arrow et al., 1996; Becker, 1976). For example, households exposed to risk of COVID-19 infection in schools might be more likely to limit social gatherings, wash hands more frequently, and wear masks more consistently. Likewise, school-based gatherings are likely to occur in regulated settings that may be less risky than some unregulated settings, such as at-home childcare, or other informal gatherings. There are also potential disparities in social distancing during school closures. For example, in California, elementary school and Hispanic children had more social contacts during school closures then high school and non-Hispanic children, respectively (Head et al., 2021). In addition, knowledge of the virus has improved over time, and mitigation measures by schools have been responsive to this new information (Jack and Oster, 2023).

Despite potential increased risk of COVID-19 transmission, in-person school has at least four benefits. First, prolonged school closures may reduce long-term human capital formation and exacerbate disparities in educational attainment between high- and low-income populations (Chetty et al., 2020; Bacher-Hicks et al., 2021; Jack et al., 2022; Halloran et al., 2021). During the pandemic, students were found to be five months behind in mathematics and four months behind in reading. As a result, lifetime earnings for these students may be reduced by as much as $49,000 to $61,000, and the impact on the US economy could amount to $128 billion to $188 billion each year (Dorn et al., 2020). Second, schools are a critical food source and provider of nutrition assistance for children (Poole et al., 2021). Third, schools are an important source of health care for children, and school-based health centers are associated with improved health care and preventive services and better health outcomes (Martin and Sorensen, 2020). Finally, schools provide critical childcare functions that allow parents to engage in the workforce (National Academies of Sciences, Engineering, and Medicine 2020). There are also critical equity concerns given that children from low-income families often depend more on school-based services than higher-income families (Donohue and Miller, 2020). Related work using mobile phone data shows that school closures in September and December 2020 were more likely to occur in schools that have higher shares of students from racial/ethnic minorities, have limited English proficiency, and are eligible for free or reduced-price school lunches (Parolin and Lee, 2021).

A key empirical challenge to examining the impacts of school closure and reopening policies on COVID-19 risk is the non-uniform nature of school closures and reopenings. While some schools fully returned to in-person instruction, other schools implemented hybrid models, with a mix of in-person and remote teaching. As of March 2021, several large school districts (e.g., Chicago, Seattle, and San Francisco) had not completely returned to in-person instruction (Issa, 2021). In addition, within many school districts, public and private schools often operate differently, with some private schools reopening while public schools remain closed (Carpenter and Dunn, 2021).

In this paper, we leverage two large sources of data to examine how school reopenings affected the spread of COVID-19. We first leverage mobile phone tracking data provided by SafeGraph. SafeGraph collects global positioning system (GPS) data from approximately 45 million U.S. mobile phones. The SafeGraph data has been used in several prior studies to measure social distancing behaviors or trends in visits to specific locations during the COVID-19 pandemic (Allcott et al., 2020; Dave et al., 2021; Goolsbee and Syverson, 2020; Cantor et al., 2022). A unique feature of the SafeGraph data is the ability to identify the number of visits to specific locations, which are mapped to industry codes (e.g., NAICS code 622110 identifies “General Medical and Surgical Hospitals”). We use the industry code for schools to measure weekly county-level visit patterns to primary and secondary schools, using an approach similar to that of Goolsbee and Syverson (2020).¹ This approach allows us to identify geographic and temporal variation in visits to schools during the COVID-19 pandemic. We use this linkage to construct visit measures for approximately 131,000 U.S. schools spread across 94 % of US counties.

We then link the county-level schools visits data to medical claims data collected from a nationwide sample of approximately 7 million individuals (3 million households) with employer-sponsored health insurance. The medical claims information allows us to identify the occurrence and timing of individual COVID-19 diagnoses and tests. Return to in-person schooling may be enabled by increased testing, and thus changes in COVID-19 diagnoses results may be due to improved detection of asymptomatic cases that would likely have gone undetected. We also examine changes in COVID-19-related hospitalizations and, as a sensitivity test, medical spending. As of December 9, 2020, we observe approximately 93,000 patients with COVID-19 diagnoses, including 10,255 children and 82,180 adults, and 7851 COVID-related hospitalizations. An important limitation of this data is that we do not observe households covered by public insurance or without insurance.

Even with this linkage, measuring the causal effect of school visits on risk of COVID-19 infection is challenging given the endogenous nature of school reopenings. Schools may be less likely to reopen when population-level COVID-19 cases and the risks of transmission are highest or trending upwards. In addition, several school districts reopened but then closed following increases in community cases (Shapiro, 2020). Thus, measuring the effect of school reopenings by comparing COVID-19 hospitalizations or cases between reopened and non-reopened schools, or gradients of reopening using school visits data, is likely to lead to biased results.

Instead, we leverage a unique feature of the medical claims data that allows us to identify households and household composition. The employer-sponsored insurance plans represented in our data provide both individual and family health insurance coverage. For family coverage policies, all covered individuals are linked to the same household plan. We use this linkage to identify household units. Under the assumption that families with school age children are more likely to be exposed to school-based COVID-19 transmission, we use a triple-differences model to compare how changes in school visits within a county over time lead to changes in household-level COVID-19 infection rates for households with and without school age children within the same county.

We find that increased school visits lead to increases in COVID-19 hospitalizations and infections for households with children, relative to households without children. However, the increase is modest in magnitude. Our results imply that a one-log unit increase in school visits leads to a 0.03 per 10,000 households increase in a household’s risk of COVID-related hospitalization and a 0.4 to 2.1 per 10,000 households increase in a household’s risk of COVID-19 infection. Based on the distribution of school visits and baseline infection rates during the COVID-19 pandemic, these results imply that moving from the 25th percentile of school visits to the 75th percentile leads to a 3 % to 18 % relative increase in risk of COVID-19 infection, depending on the specification. As a point of comparison, the reduction in school visits of the magnitude induced by county-level shelter-in-place (SIP) policies leads to a 1.3 % decrease in household COVID-19 infection rates.

Our main identification assumption relies on a lack of spillovers from school reopenings from households with children to households without children, which will lead to a downward bias in our estimates. As a test of this assumption, we decompose the triple-differences estimate into separate difference-in-differences regressions for households with and without children. If the entirety of the effect of school reopenings among households without children represents spillover effects, then we can use these difference-in-difference estimates as an upper bound of our estimates on the effect of school reopenings among households with children. In the separate difference-in-differences regressions, we find larger changes in COVID-19 hospitalizations and diagnoses for households classified as having child household members than without child members. We likewise estimate event study tests that examine differences between counties with the lowest and highest changes in school mobility. We find households with and without children in counties in the bottom tercile of changes in school mobility, relative to households in the top tercile of school mobility changes, have no difference in COVID-19 outcomes.

These results are robust to several additional tests, including controls for other policy changes that may be correlated with restricted visits to schools, mobility for other sources of transmission, variation in the intensity of the COVID-19 pandemic, and unobserved household-level differences that may impact risks of COVID-19 transmission. In additional tests, we find that our results are robust to the exclusion of summer months. We also find that increased school visits were associated with higher transmission during the initial months of the COVID-19 pandemic (March to June). Increased school visits were not associated with increased infections when COVID-19 prevalence was lower, and the virus was less contagious. Nearly all of the main effect is driven by higher transmission rates during the later months (September to December). We also find that school visits have larger effects on infection rates in counties in the top quartile of COVID-19 prevalence. Our results are also robust to an alternative data source of in-person schooling rates collected by the COVID-19 School Data Hub (“COVID-19 School Data Hub” 2023). Finally, our results are robust to a dynamic event study approach that addresses potential bias from both potential heterogeneous treatment effects and differential timing of school-related changes in mobility (Goodman-Bacon and Marcus, 2020; Sun and Abraham, 2020).

We also find that the increases in school-based COVID-19 hospitalizations and transmission are driven by households that reside in counties in the bottom income quartiles. This finding is particularly relevant, as it suggests that the socioeconomic disparities observed in the impacts of the COVID-19 pandemic also exist for school reopening policies (Parolin and Lee, 2021). Because our data comes from households covered by employer-based insurance, our results likely understate the income-based disparities in COVID-19 infections and hospitalizations. At the same time, students from lower-income households are more likely to have learning disruptions than students from higher-income households, leading to concerns about growing disparities in childhood education (Bacher-Hicks et al., 2021; van de Werfhorst, 2021; Musaddiq et al., 2022; Jack and Oster, 2023). In addition to within-household transmission originating from schools, another concern is increased risk of infection for teachers and school staff following school reopenings (Vlachos et al., 2021). However, we find that increased school visits are not associated with increased transmission rates for households in which the primary insurance subscriber is employed by a firm in the education industry relative to other industries.

Our findings inform the ongoing policy debate on school closures and reopenings (Goldhaber-Fiebert et al., 2020; Lordan et al., 2020). Our findings suggest that school reopenings contribute to COVID-19 transmission, but the magnitude of the effect is modest. When compared to other epidemiological literature on school-related risks, our estimated effects are comparable to rates of child emergency department admissions for school-related injuries (Zagel et al., 2019). Likewise, the average cost for administrating school-based mitigation strategies to properly combat COVID-19 transmission ranges from $55 to $442 per student (Rice et al., 2020). Policymakers, households, and educators should weigh the modest risks of COVID-19 transmission combined with the limited costs of implementing mitigation strategies within schools against the significant benefits of in-person schooling.

The rest of the paper proceeds as follows. Section 2 provides an overview of the existing evidence on school-related COVID-19 transmission. Section 3 describes the data used in the study. Section 4 presents our empirical approach. Section 5 reports our main results, and Section 6 presents additional results that serve as robustness checks. Section 7 concludes.

2. Background on school-related COVID-19 transmission

COVID-19 infections are less harmful for children when compared to adults (Rabinowicz et al., 2020). For example, the CDC estimates that compared to adults 40 to 49 years of age, children 5 to 17 years of age have 160 times lower risk of death from COVID-19 and 27 times lower risk of hospitalization from COVID-19 (CDC, 2020). The lower harm from COVID-19 in children and the reduced risk of contracting COVID-19 has led to a larger policy debate on school closures and transmission of COVID-19 (Christakis et al., 2020; Dooley and Christakis, 2021). The American Academy of Pediatrics encouraged in-person education during the pandemic (American Academy of Pediatrics, 2021). Nevertheless, an early report by the National Academies of Sciences, Engineering, and Medicine (2020) concluded that there is limited evidence on how easily children and youth contract the virus, how contagious they are once they do, and what strategies for limiting transmission within a school setting are most effective. The limited evidence made it difficult to both assess the health risks of opening schools and to develop strategies for limiting transmission of the virus once open.

Existing empirical studies that examine the impact of school reopenings or closures are limited and have generally found mixed results. Early data from two U.S. states finds that school districts offering hybrid or in-person instruction are not a significant contributor to COVID-19 spread in communities with low case rates (Goldhaber et al., 2022). A national study finds that school closures in the U.S. between March and May 2020 were associated with a decline in COVID-19 incidence and mortality, and that the magnitude of the effect varied based on the cumulative incidence of COVID-19 (Auger et al., 2020). On the other hand, a later study finds that a one-day increase in school closures is associated with a 3.5 % reduction in COVID-19 cases and a 3.8 % reduction in COVID-19 deaths (Zimmerman and Anderson, 2021).

Other studies using the same mobility data find increases in community spread following school reopenings (C. J. Courtemanche et al., 2021; Chernozhukov et al., 2021). We extend these studies by focusing our identification strategy on a triple-differences approach, examining heterogeneous effects of school closures based on COVID-19 prevalence and income differences, and estimating the impact of social distancing policies on school visits. The SafeGraph data also allow us to construct measures of changes in non-school mobility that may simultaneously impact COVID-19 spread, including bar/restaurant mobility and changes to all sources of non-school mobility. Our approach and data allow us to more cleanly isolate the impacts of changes in school reopening policies COVID-19 outcomes, including hospitalizations, infections, and deaths. Our data also allow us to explore how these impacts changed over the course of the pandemic and differentially impacted vulnerable populations. Finally, we use observed changes in physical mobility to schools following the implementation of social distancing policies to estimate the impacts of social distancing policies on school-related COVID-19 infections and hospitalizations.

Studies from other countries also find mixed results, with some studies finding no changes in COVID-19 transmission (Isphording et al., 2021) and other studies finding increased infection rates (Vlachos et al., 2021). Many of these studies compare infection rates between countries, which could have different risk mitigation policies. A related literature examines the impact of college openings on transmission and finds that reopening in-person instruction leads to increases in transmission (Andersen et al., 2020). However, this evidence may not generalize to school reopenings given the large differences in the number of visits, living conditions, and risk of infection for college versus K-12 school student populations.

An important limitation of many of these studies is the lack a within-market control group that can help account for endogenous school reopenings and the within-market trajectory of the pandemic. Existing papers also contain limited controls for other sources of COVID-19 transmission. Our empirical approach, described in detail below, leverages household composition to construct within-market control groups. An important challenge to this approach is the potential of spillovers from households with children to households without children. We also explore the impact of other sources of COVID-19 transmission, including other forms of social gatherings and other risk mitigation policies.

3. Data

3.1. Number of school visits to measure school-based physical mobility

A challenge with examining the effect of school reopenings and COVID-19 transmission is the lack of nationwide data on school reopenings. To address this limitation, we use phone mobility data provided by SafeGraph. The SafeGraph data aggregates global positioning system pings from approximately 45 million mobile phones. The data are from mobile applications that obtain opt-in consent from users to collect anonymous location data. These data have been used to track the number of visits to businesses (Goolsbee and Syverson, 2020; Crane et al., 2022), and health care professionals (Cantor et al., 2022). The data have also been used to track school closures across the U.S. (Parolin and Lee, 2021). Within the SafeGraph data, we identify elementary and secondary schools using NAICS code 611,110 for “Elementary and Secondary Schools”. This process identifies 131,080 U.S. schools located in 3059 counties. Then, using the data, we collapse the total number of visits at the week-year level for each county. We use all visits to schools to measure visits to schools. As a sensitivity test, we also restrict visits to those lasting at least four hours.

With the mobile phone data, we use a modified version of the approach outlined in Goolsbee and Syverson (2020) and calculate the log-transformed county-level difference in the number of visits to schools between each 2020 week and the same week in 2019. For each county $g$ and week $t$, we calculate

$$\ln \mathrm{\Delta }schoo{l}_{gt}=\ln \left(schoo{l}_{gt2020}\right)-\ln \left(schoo{l}_{gt2019}\right)$$ (1)

This approach effectively measures the weekly percent change in visits to schools for each county relative to pre-pandemic levels.

We present distributions of each measure across counties in Fig. 1, using kernel density plots for the weeks of March 1, May 10, and September 27, 2020. The distribution of the main measure, the difference in the natural log number of visits in 2020 and 2019, is clustered around zero for the week of March 1, 2020 (mean = 0.35, SD = 0.57). By the week of May 10, 2020, the first week of the pandemic, the distribution is significantly skewed, showing large declines in the difference in the number of visits (mean= −1.48, SD = 0.62). By September 27, 2020, the number of visits is again distributed around zero (mean= −0.30, SD = 0.62).

Fig. 1.

Distribution of log-transformed school visit measures.

Fig. 2 maps geographic variations in the school visit measure. There is substantial geographic variation in the county-level visits measures for the three weeks of March 1, May 10, and September 27, 2020. Areas shaded in blue exhibited the smallest declines in school visits, which would indicate school closures. This geographic variation in the intensity of school reopenings following the initial closure underlies our empirical approach.

Fig. 2.

Geographic distribution of log-transformed school visits.

3.2. Medical claims data

Our data on COVID-19 related outcomes come from medical claims data from approximately seven million people collected by Castlight Health, which provides a health benefits and price transparency platform to approximately 200 employer-sponsored insurance plans. For participating employers, the data includes medical and pharmacy claims for all employees and their dependents. A unique feature of the data is that it allows for a linkage of members to households for households with a family insurance plan. Participating employers represent a wide range of industries, including education, transportation, retail, and financial services, and employees are located in all U.S. states. These data have been previously used to track health care utilization during the pandemic (Whaley et al., 2020), and existing studies have found that this population is representative of the broader U.S. population with employer-sponsored insurance (Cantor et al., 2022).

For each household, we identified any COVID-19 diagnoses in that week using ICD-10 codes U07.1, B34.2, and B97.29. Other studies have found that the sensitivity and specificity of these administrative diagnosis codes for COVID-19 are 98.0 % and 99.0 %, respectively (Kadri et al., 2020). An important limitation of using clinical diagnoses for COVID-19 is that we potentially miss asymptomatic cases or infections that do not require interactions with health care providers. Thus, our results can be interpreted as the effect of county-level school visits on moderate-to-severe COVID-19 infections. Due to a lag period of when a medical event occurs and the completeness of the medical claims data, we used data through the 46th week of 2020, ending on November 15, 2020.

A potential challenge for using diagnoses as a primary outcome is the possibility that school reopening policies include testing strategies to mitigate COVID-19 spread. Such testing is likely to catch asymptomatic COVID-19 cases that would have remained undiagnosed in the absence of increased testing. In such a case, it is challenging to test if our results reflect increased COVID-19 transmission or simply more accurate diagnoses. As a solution to this challenge, we use COVID-19-related hospitalizations as our primary dependent variable, with infection rates as a secondary outcome. Hospitalizations are unlikely to reflect testing strategies, as COVID-19 cases that require hospitalization are unlikely to be induced by an increase in testing (Harris et al., 2021). As an additional outcome for supplementary analyses, we also measure household spending on COVID-19 care, which we construct by summing costs for all medical claims with a COVID-19 diagnosis or procedure code. We include all COVID-related spending, including spending by patients and spending by the employer/insurer. Measuring impacts on spending allows an approximation of the health care costs of school reopenings (Harris et al., 2021).

Table 1 describes characteristics of households with (N = 790,237, 28.5 % of sample) and without (N = 790,237, 71.5 % of sample) children. For each characteristic, we report the standardized difference between the two household types. The mean COVID-19 infection rates, as well as the geographic and industry composition of households with and without children are relatively similar, with most standardized differences below a 0.1 standard deviation difference. Table A1 shows that the Castlight sample is broadly representative of the employer-sponsored insurance population.

Table 1.

Descriptive characteristics of study population.

	Household without children		Household with children
	Mean	SD	Mean	SD	Standardized difference
Any household COVID hospitalization ( %)+	0.27 %	5.19 %	0.32 %	5.62 %	−0.009
Any household COVID diagnosis ( %)+	2.58 %	15.84 %	3.96 %	19.51 %	−0.08
COVID-related medical spending ($)+	$83.6	$3962.0	$80.7	$5197.0	<0.01
Number of household members	1.67	1.06	3.85	1.28	−1.86
Census region ( %)
Pacific	19.16 %	39.35 %	20.09 %	40.07 %	−0.02
Mountain	5.94 %	23.63 %	5.52 %	22.84 %	0.02
West north central	5.93 %	23.63 %	5.79 %	23.35 %	0.01
West south central	3.07 %	17.24 %	2.82 %	16.56 %	0.01
East north central	18.54 %	38.86 %	18.70 %	38.99 %	0.00
East south central	30.74 %	46.14 %	29.47 %	45.59 %	0.03
New England	6.74 %	25.07 %	6.61 %	24.84 %	0.01
South Atlantic	9.90 %	29.86 %	11.00 %	31.29 %	−0.04
Industry of primary subscriber ( %)
Aerospace & Defense	9.38 %	29.16 %	8.92 %	28.51 %	0.02
Apparel	0.11 %	3.33 %	0.13 %	3.58 %	0.00
Automotive	5.04 %	21.87 %	5.76 %	23.30 %	−0.03
Chemicals	0.25 %	4.97 %	0.26 %	5.11 %	0.00
Construction	0.67 %	8.13 %	0.85 %	9.18 %	−0.02
Education	2.17 %	14.56 %	2.26 %	14.88 %	−0.01
Electronics	1.51 %	12.18 %	1.01 %	10.00 %	0.04
Engineering	0.07 %	2.59 %	0.09 %	3.08 %	−0.01
Entertainment & Hospitality	0.14 %	3.76 %	0.11 %	3.34 %	0.01
Financial Services	6.64 %	24.90 %	8.16 %	27.38 %	−0.06
Food & Beverage	4.36 %	20.42 %	5.41 %	22.62 %	−0.05
Government	9.53 %	29.37 %	8.91 %	28.50 %	0.02
Grocery	4.07 %	19.77 %	3.19 %	17.58 %	0.05
Hospitals & Healthcare	5.55 %	22.90 %	5.90 %	23.56 %	−0.01
Insurance	2.92 %	16.84 %	3.26 %	17.75 %	−0.02
Legal Services	0.05 %	2.16 %	0.04 %	1.96 %	<0.01
Manufacturing	6.80 %	25.17 %	6.52 %	24.70 %	0.01
Media	0.05 %	2.34 %	0.04 %	2.04 %	0.01
Medical Devices	0.42 %	6.45 %	0.54 %	7.33 %	−0.02
Missing	0.18 %	4.28 %	0.13 %	3.63 %	0.01
Non-Profit	0.24 %	4.91 %	0.28 %	5.29 %	−0.01
Oil, Energy, & Utilities	2.26 %	14.86 %	3.22 %	17.66 %	−0.06
Other	0.48 %	6.94 %	0.45 %	6.68 %	0.01
Pharmaceuticals & Biotech	0.39 %	6.22 %	0.77 %	8.73 %	−0.05
Professional Services	2.08 %	14.27 %	1.37 %	11.63 %	0.05
Real Estate	0.08 %	2.85 %	0.10 %	3.21 %	−0.01
Retail	18.72 %	39.01 %	13.91 %	34.60 %	0.13
Security	0.79 %	8.85 %	0.21 %	4.60 %	0.08
Semiconductors	0.89 %	9.38 %	1.78 %	13.23 %	−0.08
Software & Technology	0.33 %	5.72 %	0.42 %	6.46 %	−0.02
Telecommunications	11.95 %	32.43 %	14.26 %	34.97 %	−0.07
Transportation	1.90 %	13.67 %	1.71 %	12.98 %	0.01

⁺Over course of entire study period

3.3. COVID-19 social distancing policies and exposure data

We use data on county-level shelter-in-place policies that was collected by Cook et al. (2020). To construct these data, the authors follow three steps. First, the authors collected the dates for statewide orders. Second, for states that lacked a state-wide order, the authors determined whether an individual county had a shelter-in-place policy by searching local news and government sites. Finally, the counties for which the authors did not find information on a shelter-in-place policy were assumed to have followed the state’s guidance (Cook et al., 2020). Because many of these policies were enacted in response to COVID-19 cases and deaths, we also collected data on COVID-19 incidence rates from USAFacts, which aggregates CDC data (USAFacts, 2020). The USAFacts data have the total number of cases and deaths in each county for each day.

4. Empirical approach

With these data, we estimate the effect of school reopenings using within-county variation in foot traffic to schools and household structure. We estimate the effects of changes in school visits on COVID-19 outcomes using a triple-differences model of the form:

$$\begin{gathered} covi{d}_{igt}=\alpha +{\gamma }_{1}chil{d}_i+\delta chil{d}_i\times \mathrm{\Delta }schoo{l}_{gt-2}+member{s}_i \\ +\tau wee{k}_t+\psi count{y}_g+\psi count{y}_g\times \tau wee{k}_t+{\epsilon }_{igt} \end{gathered}$$ (2)

In this model, $covi{d}_{igt}$ represents the COVID-19 related outcomes of interest—an indicator for COVID-19 hospitalization and an indicator for COVID-19 diagnosis for household $i$ in county $g$ during week $t$. As an additional sensitivity test, we also measure log-transformed COVID-19 spending. The $chil{d}_i$ term indicates that the household has a school-age child. The $\mathrm{\Delta }schoo{l}_{gt-2}$ represents the week and county-specific measure of visits to schools from the SafeGraph data. Given the incubation period of the SARS-CoV-2 virus, we use a two-week lag between changes in the number of visits to schools and household-level outcomes. As a sensitivity test, we also use a one-week lag and find similar results. To adjust for differences based on household composition, we control for the number of people enrolled on a household’s insurance plan ($member{s}_i$). The $wee{k}_t$ fixed effects account for the nationwide trajectory of the COVID-19 pandemic, while the $count{y}_g$ fixed effects account for time-invariant county-level differences in exposure risk. We also add fixed effects for county-by-week interactions ($count{y}_g\times wee{k}_t$), which account for time-varying trends at the county level. This specification absorbs any broader changes in county-specific policies (e.g., mask mandates and shelter in place policies), COVID-19 spread, or changes in physical mobility. This measure also absorbs our main effect of school-related visits ($\mathrm{\Delta }schoo{l}_{gt-2}$). Within a given county, it isolates the differential impact of changes in school-related visits between households with and without children. To further isolate changes related to schools, we also iteratively add a similar children-by-week interaction fixed effect ($chil{d}_i\times wee{k}_t$), which accounts for any non-school mobility related changes in child-specific COVID-19 risks throughout the study period.

Our primary coefficient of interest, $\delta$, captures the differential change in COVID-19 outcomes between households with and without children following changes in county-level visits to school. In all specifications, we include fixed effects for week and county. Thus, the $\delta$ coefficient measures the change in COVID-19 infections between households with and without children in the same county, and relative to all other households in that week. Due to these fixed effects and because our school visits measures are county and week specific, we do not include main post-reopening or treatment county indicators. We estimate all models using ordinary least squares and cluster standard errors at the county level.

Across all specifications, the $\delta$ coefficient measures the intent-to-treat effect of changes in county-level school visits on COVID-19 diagnoses and other COVID-19 related outcomes. We are unfortunately unable to link data on household-specific school visits and infections, which would allow us to fully estimate the first-stage effect that would allow for a local-average treatment effect estimate of the direct effect of school visits on COVID-19 cases. We are also unable to account for differences in school-specific policies designed to limit infection spread (e.g., mask and social distancing stringency), which are important contributors to mitigating the spread of COVID-19 (Boutzoukas et al., 2022). Instead, this estimate captures both the direct effect of school-related COVID-19 transmission (e. g., children becoming infected at school) and the potential indirect effect of risk avoidance by households and schools.

Our identification strategy compares trends in COVID-19 hospitalizations and diagnoses for households with and without children, which we measure using household insurance enrollment structures. This approach faces two empirical challenges. The first empirical challenge is the potential endogeneity of changes in school visits. Schools may be less likely to reopen in areas with high COVID-19 prevalence. Our approach of comparing infection rates between households with and without children within the same county attempts to address the endogeneity of school reopenings, but leads to a second empirical challenge.

Our primary identification assumption is that school visits impact households with children but not our within-county control group of households without children. Potential threats to this assumption include infection spillovers from households with children to those without children, which will bias our estimates towards zero, or unobserved risk mitigation approaches (e.g., mask wearing) implemented by households with children and not households without children, which will bias our estimates upwards. Testing these individual potential sources of bias is empirically challenging. As a solution, we attempt to bound the magnitude of potential spillover effects, which are present in the $\mathrm{\Delta }schoo{l}_{gt-2}$ coefficient in our estimated regressions.

To do so, we add controls that plausibly adjust for both spillover effects and the endogeneity of school reopenings with COVID-19 infection rates. First, we control for policies designed to address COVID-19 spread and other potential sources of COVID-19 transmission. Specifically, we control for the introduction of county-level shelter-in-place policies. These policies are designed to slow COVID-19 spread, and may impact the rate of infection in a county (C. Courtemanche et al., 2020; Berry et al., 2021). We also control for visits to other locations—bars and restaurants—associated with increased COVID-19 risk. We construct similar measures of number of visits to bar and restaurant locations in the SafeGraph data. Social gatherings at bars and restaurants are an important potential source of COVID-19 infection transmission (Pray et al., 2021). To measure total physical movement occurring within a county for a given week, we construct measures of weekly changes in visits to all locations in a county, excluding schools. We define these as any location without the school NAICS code (611110). We also interact fixed effects for the industry of the primary insurance subscriber’s employer with week fixed effects. These industry-by-week fixed effects control for industry-specific shocks that lead to differences in COVID-19 transmission, such as the ability to work remotely.² Each of these additional controls address potential confounders that are related to both county-level school-related visits and COVID-19 spread. Finally, we also include household fixed effects to control for time-invariant differences in COVID-19 risk across households.

As an additional sensitivity test, we decompose the triple-differences estimate into separate difference-in-differences regressions for households with and without children. Doing so allows us to assess the validity of our triple-differences approach, and test for potential contamination of the control group, which will lead to a downward bias on our estimates. This test compares the effects of school reopenings among households with children compared to households without children. If the effect of school reopenings among households without children represents potential spillover effects, we can use these estimates to bound estimates for the effect of school reopenings among households with children. In the separate difference-in-differences regressions, we find much larger changes in COVID-19 hospitalizations and diagnoses for households with children than without children.

As discussed below, we also estimate several additional tests that examine differences within counties and between different types of households. We estimate models that non-linearly test the effects of changes in county-level school visits on COVID-19 infections. We also test for differences based on COVID-19 prevalence in a county. We finally separately estimate event studies that test for trends in COVID-19 infections based on county-level school visits.

As an additional test, we also estimate “dynamic” event studies that account for potential bias due to differences in the timing of school-related mobility changes and potential treatment effect heterogeneity (Goodman-Bacon and Marcus, 2020; Goodman-Bacon, 2021). However, an important challenge is the continuous nature of our school mobility treatment measure. To address this challenge, we construct binary measures of changes in school mobility by categorizing the 2019 to 2020 change in school-based mobility measure in each county ($\mathrm{\Delta }schoo{l}_{gt}$) into terciles. When categorizing, we take the mean of the weekly measure, and thus measure aggregate changes in school mobility across the 2020 study period. We then apply the Sun-Abraham estimator and estimated event studies that compare changes in our COVID-related outcomes between counties in the top and bottom terciles of changes in school-based mobility. As discussed in the Appendix, this approach is consistent with our main results.

5. Main results

5.1. Effect of school visits on COVID-19 hospitalizations and diagnoses

Table 2 presents our main results that measure the effect of visits to schools on COVID-19 hospitalizations and diagnoses. To allow for an easier comparison with epidemiological studies of the COVID-19 pandemic, we express hospitalization and diagnosis probabilities in per 10,000 household units. For hospitalizations (column 1), we find that a one-log increase in visits to schools leads to a 0.03 per 10,000 households increase in COVID-19 hospitalizations. Adding the $chil{d}_i\times wee{k}_t$ fixed effects removes the statistical significance of the coefficient (column 2). We likewise find a 0.4 per 10,000 households increase in COVID-19 infections (column 3) that increases to a 2.1 increase after accounting for differential time trends among households with children (column 4). These reductions among households with children are consistent with lower infection and severity rates among younger individuals. We report the supplementary analyses on COVID-19 spending in Appendix Table A2. We find no change in COVID-19 spending using our main specification.

Table 2.

DDD estimates on the effect of school visits on household COVID-19 hospitalizations, and diagnoses.

	(1) COVID Hospitalization	(2)	(3) COVID Diagnosis	(4)
Child in household × Δschoolgt−2	0.0287** (0.0141)	−0.0473 (0.0410)	0.369*** (0.0863)	2.100*** (0.374)
Child in household	−0.481*** (0.0334)		−2.563*** (0.148)
Number of household members	0.277*** (0.0155)	0.27*** (0.0154)	2.853*** (0.1000)	2.853*** (0.1000)
Observations	127,598,848	127,598,848	127,598,848	127,598,848
county X week FE	X	X	X	X
child in household X week FE		X		X
Mean value	0.7		8.7

This table presents regression results from Eq. (3) and measures effect of county-level school visits on the weekly change in household COVID-19 hospitalizations, and diagnoses between household with and without children. Standard errors clustered at the county-level in parentheses. Hospitalization and diagnosis coefficients and standard errors are multiplied by 10,000 and can be interpreted as the change in weekly rates per 10,000 households.

^***p < 0.01.

^**p < 0.05.

^*p < 0.1.

For COVID-19 infection rates, our results of 0.4 to 2.1 increased weekly cases per 10,000 households represent 4.5 % and 27 % increases relative to the weekly median household diagnosis rate between the 10th and 46th weeks of 2020 of 7.8 cases per 10,000 households. During the same period, the median difference between the 75th and 25th percentiles of school visits is 0.67 log units. Thus, a move from the 25th percentile to the 75th percentile of school reopenings is associated with 3.2 % to 18 % percent increases in COVID-19 cases, depending on the specification.

The estimates in Table 3 attempt to control for potential bias from endogenous school reopenings by including covariates that are likely correlated with both COVID-19 transmission and school reopenings. Because this table aims to test the sensitivity of the school mobility coefficient to the inclusion of additional controls for other policies introduced at the county-level, we omit the $count{y}_g\times wee{k}_t$ fixed effect interactions. Columns 1 and 4 are the most parsimonious and include just the main treatment variables and controls for the number of household members, week fixed effects, and year fixed effects. The next columns (2 and 5) add covariates for other policies and forms of mobility (e.g., shelter-in-place policies, mobility to non-school locations, fixed effects for the number of weeks since the first COVID-19 case and death in a county, and week-by-industry interaction fixed effects). The final set of columns (3 and 6) add household fixed effects. For each of the outcomes, we find that including the additional controls leads to large reductions in the school mobility coefficient magnitude for the likelihood of COVID-19 related hospitalizations. Adding the household fixed effects further reduces the school mobility coefficient magnitude and precision, including for the likelihood of COVID-19 diagnosis. The results in Table A3 show that our findings are robust to using a single lag period.

Table 3.

Sensitivity of DDD estimates to alternative controls.

	(1)	(2)	(3)	(4)	(5)	(6)
	COVID Hospitalization			COVID Diagnosis
Child in household × Δschoolgt−2	0.0328** (0.0140)	0.0407*** (0.0140)	0.0536*** (0.0136)	0.432*** (0.0874)	0.479*** (0.0841)	0.221*** (0.0636)
Δschoolgt−2	0.311*** (0.0425)	0.130*** (0.0378)	0.0676* (0.0387)	1.987*** (0.337)	1.824*** (0.348)	1.114*** (0.232)
Child in household	−0.440*** (0.0302)	−0.427*** (0.0299)		−2.308*** (0.159)	−2.274*** (0.155)
Number of household members	0.248*** (0.0134)	0.242*** (0.0131)		2.639*** (0.0912)	2.642*** (0.0901)
SIP policy		0.127* (0.0680)	0.267*** (0.0795)		0.624 (0.639)	1.349*** (0.464)
Bar mobility		0.329* (0.176)	0.158 (0.189)		−2.365* (1.354)	−1.295 (1.265)
Restaurant mobility		−0.0524 (0.0320)	−0.0667** (0.0310)		−0.758*** (0.292)	−0.619** (0.261)
Non-school mobility		0.222 (0.148)	0.0538 (0.142)		3.497*** (1.225)	−0.0353 (1.046)
Observations	127,601,976	127,601,976	127,601,976	127,601,976	127,601,976	127,601,976
SIP policy		X	X		X	X
Other transmission sources		X	X		X	X
HH FE			X			X
Mean value	0.7			8.7

This table presents regression results from Eq. (3) and measures effect of county-level school visits on the weekly change in household COVID-19 hospitalizations, diagnoses, and medical spending between household with and without children. Standard errors clustered at the county-level in parentheses. Within each outcome, the first column includes controls for the number of household members; the second column adds controls for shelter-in-place policies, foot traffic to bars, restaurants, and all non-school locations; and the third column adds household fixed effects. Hospitalization and diagnosis coefficients and standard errors are multiplied by 10,000 and can be interpreted as the change in weekly rates per 10,000 households.

^***p < 0.01.

^**p < 0.05.

^*p < 0.1.

Table A4 decomposes the triple-differences regression into separate difference-in-differences regressions for households with and without children. As in Table 3, because we are focused on the coefficient for changes in school mobility, we are unable to include the $count{y}_g\times wee{k}_t$ fixed effect interactions, and so the results are not fully comparable to our main results in Table 2. These results also do not include the within-county control group comparison, and so the causal interpretation of these results is limited. When including the full set of controls, we do not find an association between county-level changes in school mobility and COVID-19 related hospitalizations among households without children (column 2). In contrast, we do find a positive association among households with children on COVID-19 related hospitalizations. We find an increase in COVID-19 infections among households with (column 8) and without (column 6) children. Among COVID-19 infections, we find a 0.9 and 1.9 per 10,000 households increase following a one log-unit increase in school mobility, among households with and without children. However, the estimated associations without the full set of controls are approximately twice the size when including controls for alternative sources of transmission. This difference suggests school mobility is endogenously related to other policies and COVID-19 transmission risks, and further supports including the within-county controls of households without children.

6. Impact of social distancing policies on school visits

We finally examine how changes in the number of school visits have responded to policies designed to limit social interactions. Understanding the behavioral responses to these policies allows for a “first stage” estimate that shows the size of the change in the number of weekly visits to schools after a shelter-in-place policy went into effect. To do so, we use the SafeGraph data and estimate the effect of social distancing policies on school visits using a two-way fixed effect model of the form:

$$\ln \left(visit{s}_{jgt}\right)=\alpha +\delta polic{y}_{gt}+\tau wee{k}_t+\tau yea{r}_t+\psi schoo{l}_i+{\epsilon }_{jgt}$$ (3)

This regression measures the change in log-transformed mobility to school $j$ in week $t$ before and after the implementation of a social distancing policy in county $g$. We include fixed effects for week and for the 131,000 schools identified in the SafeGraph data based on their NAICS code. Unlike the other analyses, where we use just 2020 data and measure week-level changes in 2020 school visits relative to the same week in 2019, we use school visit data for both 2019 and 2020. We include a fixed effect for 2020, which allows us to estimate the changes in within-school visits between 2019 and 2020 for each calendar week.

As shown in Table 4, the introduction of county-level social distancing policies leads to a 0.28 log-unit change in school visits. This estimate is unchanged when including fixed effects for year-by-week interactions to control for week-specific changes in school visits and state-by-week fixed effects to control for temporal changes within states (e.g., state-level exposure to the COVID-19 pandemic). Tying these results to our earlier results suggests that a decrease in school visits equivalent to the reduction induced by the introduction of social distancing policies leads to a 0.08 per 10,000 (0.0008 percentage point) decrease in the risk of household-level COVID-19 infection and a 0.1 per 10,0000 household decrease in COVID-19 hospitalizations. Based on the baseline mean of rate COVID-19 diagnoses and hospitalizations per 10,000 households, our results imply that county-level social distancing policies lead to a 1.3 % decrease in COVID-19 infections and a 0.2 % decrease in hospitalizations.

Table 4.

Effect of county-level social distancing policies on school visits.

	(1)	(2)	(3)
Social distancing policy	−0.279*** (0.0236)	−0.282*** (0.0236)	−0.281*** (0.0237)
year 2020	−0.422*** (0.0188)		−0.421*** (0.0188)
Observations	11,307,112	11,307,112	11,307,112
R-squared	0.712	0.763	0.727
School FE	X	X	X
Week FE	X	X	X
Year-week FE		X
State-week FE			X

This table presents regression results from equation 6 and measures the effect of county-level social distancing policies on school visits. County-level social distancing policies represent shelter-in-place policies collected by Cook et al. (2020). Standard errors clustered at the county-level in parentheses.

^***p < 0.01.

^**p < 0.05.

^*p < 0.1.

7. Robustness tests

7.1. Differences based on intensity of COVID-19 pandemic

School-based COVID-19 transmission is likely to have a larger effect in areas with higher underlying rates of COVID-19 transmission. As a test of this assumption, we categorize counties into quartiles based on COVID-19 prevalence ($case{s}_g$). We assign quartiles across the entire study period. In the first quartile of cases, we not surprisingly find no change in COVID-19 hospitalizations or infection rates. Columns 2 to 4 of Table 5 show increased household-level hospitalizations and infection rates in counties with higher COVID-19 infections. In the second quartile, our DDD estimates are 0.05 and 0.2 per 10,000 households increase in hospitalizations and diagnoses, respectively. In the third and fourth quartiles, these estimates are stable for hospitalizations, but increase to increases to 2.0 and 4.3 per 10,000 households increases in infections, respectively. The fourth-quartile estimate represents an approximately 11 % relative increase in infection rates. In both specifications, the increase in school-based transmission in areas with high community spread suggests school-reopening policies should be sensitive to levels of community prevalence.

Table 5.

Differences based on quartiles of county-level COVID-19 prevalence.

	(1)	(2)	(3)	(4)
	1st quartile prevalence (0 cases per 10,000)	2nd quartile prevalence (1.3 cases per 10,000)	3rd quartile prevalence (6.7 cases per 10,000)	4th quartile prevalence (34.5+ cases per 10,000)
COVID-19
Hospitalization
Child in household × Δschoolgt−2	0.0266 (0.0368)	0.0464** (0.0201)	0.0702** (0.0349)	0.0558 (0.105)
Child in household	0.00665 (0.0200)	−0.170*** (0.0403)	−0.410*** (0.0657)	−1.531*** (0.156)
COVID-19 Diagnosis
Child in household × Δschoolgt−2	−0.0781 (0.119)	0.153** (0.0724)	1.997*** (0.161)	4.371*** (0.549)
Child in household	−0.0162 (0.0492)	−1.422*** (0.180)	−1.210*** (0.296)	−3.154*** (0.679)

This table presents regression results from Eq. (3) and measures how the effect of county-level school visits on the weekly change in household COVID-19 hospitalizations, diagnoses, and medical spending between household with and without children varies based on the prevalence of COVID-19 in that county. COVID-19 prevalence is measured in quartiles of cases. Standard errors clustered at the county-level in parentheses. Coefficients and standard errors for hospitalizations and diagnoses are multiplied by 10,000 and can be interpreted as the change in weekly rates per 10,000 households.

^***p < 0.01.

^**p < 0.05.

^*p < 0.1.

7.2. Differences across the COVID-19 pandemic

As a similar test, we next examine differential impacts across the evolution of the COVID-19 pandemic. Changes in visits to schools during the early phases of the pandemic, when baseline infection rates are low and the virus was less contagious, are less likely to contribute to transmission than changes in school visits when infection rates are high. Risk-mitigation approaches have been developed and changed over the course of the pandemic, and so the net effect of increased exposure to the pandemic on school-based transmission is unclear. To capture these changes, we separately estimated Eq. (3) for each week of 2020, through week 46. Because this test is estimated separately for each week, we exclude the time fixed effects. This test allows us to examine temporal trends in the triple-differences treatment effect and if the difference in COVID-19 outcomes between households with and without children is different between early weeks of the pandemic and later weeks.

As shown in Fig. 3, we do not find differences in COVID-19 hospitalizations (Panel A). However, we find that most of the differences in household infection (Panel B) occur in later weeks. In the first portion of 2020, we find that changes in county-level visits to schools do not lead to changes in household infection. This null finding is consistent with the previous sensitivity test, which found increased transmission rates in counties with higher COVID-19 prevalence. We find that the DDD coefficients are driven by changes that occur starting in week 40, which corresponds to the last week of September. The number of school visits is measured with a one-week lag, and so school-based visits beginning in mid-September 2020 drive our main results. By the 46th week of 2020, which corresponds to the second week of November, the estimated DDD implies that a one-unit increase in log school visits leads to an 8.5 increase per 10,000 households in COVID-19 transmission for households with children, relative to those without. This effect is more than an order-of-magnitude larger than our main results in Table 2. These results are consistent with event studies that use the Sun-Abraham (2020) estimator (Figure A3).

Fig. 3.

Estimates of the impact of school visits on COVID-19 outcomes by week.

This result, paired with the results in Table 5, suggests that the impact of school-based transmission interacts with the intensity of the COVID-19 pandemic. Not surprisingly, when overall COVID-19 risks are low, the risks of school-based transmission are also low. When community cases are high, schools are another mode of transmission, and higher levels of community spread enable higher levels of school-based spread.

7.3. Differences between high vs. low mobility change counties

As a related test, we estimate time-varying differences between counties with “high” vs. “low” changes in school mobility. To do so, we categorized counties into terciles based on the mean weekly percent change in school mobility over the post-pandemic study period. We compared differences in the COVID-19 outcomes between households with and without children in the bottom, the lowest tercile, relative to households with and without children in the top, the highest tercile counties. More specifically, we estimated event studies of the form:

$$\begin{gathered} covi{d}_{igt}=\alpha +\sum _t{\delta }_{t}hig{h}_g\times chil{d}_i+{\gamma }_{1}chil{d}_i+member{s}_i \\ +\tau wee{k}_t+\psi count{y}_g+{\epsilon }_{igt} \end{gathered}$$ (4)

Across all outcomes, we do not find differences between households with vs. without children in the “high” school mobility change counties, relative to the same comparison in the “low” mobility change counties in the initial weeks of the pandemic (Fig. 4). The coefficients are small in magnitude and centered around zero. Starting around week 20, the weekly coefficients fluctuate, but with large confidence intervals. Overall, we do not find meaningful differences in COVID-19 outcomes between our main comparison of households with and without children based on the degree of changes in school mobility during the pandemic.

Fig. 4. Weekly differences in COVID-19 outcomes between high and low school mobility change counties.

Notes: High and low mobility change counties defined as counties in the top and bottom tercile of 2020 school mobility changes. Figures present weekly differences in outcomes between households with and without children in high mobility change counties, relative to the same comparison in low mobility change counties.

7.4. Differences by county-level income composition

A substantial literature documents race and income disparities in the health and non-health impacts of the COVID-19 pandemic (Jay et al., 2020; Polyakova et al., 2021). In addition, access to in-person learning differed by student race, with racial minorities less likely to have access to full-time in-person learning (Oster et al., 2021; Fox et al., 2021). The effects of school reopenings on COVID-19 transmission may also show similar disparities. To test for disparities, we also examined differences based on the income composition of the county in which patients live. We lack information on household-level income. For income, we categorized county-level household income into quartiles using the pooled 2013 to 2018 American Community Survey (ACS).

As shown in Table 6, we find inconsistent differences in COVID-19 hospitalization based on county income. For COVID-19 diagnoses, the $chil{d}_i\times \mathrm{\Delta }schoo{l}_{gt-2}$ coefficient for households in the bottom quartile of the income distribution is 1.3 per 10,000 households, compared to 0.7 per 10,000 households for the second quartile, 0.5 per 10,000 households among the third quartile, and a non-statistically significant 0.2 per 10,000 households among the top quartile. These results show school reopening have larger adverse impacts among lower-income counties. These differences may be explained by differences in risk mitigation strategies accompanying school reopening (e.g., increased ventilation, mask policies, regular testing), which may be more prevalent in higher-income counties.

Table 6.

DDD estimates of the impact of school visits on COVID-19 infection rates by county income quartile.

	(1)	(2)	(3)	(4)
Income quartile	1st	2nd	3rd	4th
COVID-19 Hospitalization
Child in household × Δschoolgt−2	0.0637 (0.0787)	0.0920* (0.0470)	−0.0255 (0.0260)	0.0359** (0.0175)
Child in household	−0.864*** (0.137)	−0.492*** (0.0763)	−0.440*** (0.0625)	−0.452*** (0.0453)
COVID-19 Diagnosis
Child in household × Δschoolgt−2	1.069*** (0.290)	0.663*** (0.175)	0.392** (0.153)	0.138 (0.109)
Child in household	−1.756*** (0.560)	−2.126*** (0.433)	−2.273*** (0.268)	−2.915*** (0.193)

This table presents results that measure the effect of county-level school visits on household-level COVID-19 hospitalizations, diagnoses, and medical spending between household with and without children. Separate models test for differences in the first quartile (column 1), second quartile (column 2), third quartile (column 3), and fourth quartile (column 4) of county income. County income is measured using data from the American Community Survey. Standard errors clustered at the county-level in parentheses. For hospitalizations and diagnoses, coefficients and standard errors are multiplied by 10,000 and can be interpreted as the change in weekly rates per 10,000 households.

^***p < 0.01.

^**p < 0.05.

^*p < 0.1.

7.5. Robustness test excluding summer months

Our main results include observations for all weeks of 2020, through mid-November 2020. Summer months, when schools are commonly scaled back, are included in this period. Because our measure of school visits is relative to the same week in 2019, our results should be robust to summer shutdowns, as long as shutdown patterns were the same in 2019 and 2020. As an additional test, we estimate the same regression model, but exclude summer months—June, July, and August. As shown in Appendix Table A5, excluding summer months from the analysis leads to results that are slightly smaller in magnitude, but range from 0.2 to 0.3 cases per 10,000 households.

7.6. Differences between children and adults

Our main results pool children and adults, but the impacts of county-level school visits on COVID-19 outcomes may differ between children and adults. Children may be more susceptible to school-related COVID-19 transmission, but are more likely to be asymptomatic carriers (Vermund and Pitzer, 2020). Adults may be less likely to receive school-related infections, but may also be vulnerable to an infection due to school reopenings (Vlachos et al., 2021; Lessler et al., 2021). Thus, as an additional test, we estimate separate models that examine age-specific diagnoses. We test for changes in diagnoses among all children (ages 0 to 18) and all adults (ages 19 to 64) and among specific age groups (ages 0 to 4, 5 to 18, 19 to 29, 30 to 39, 40 to 49, 50 to 59, and 60 to 64).

As shown in Table A6, we find slightly larger increases in pediatric diagnoses. A one-unit increase in visits to schools leads to a 0.3 per 10,000 households increase in the likelihood of a child COVID-19 diagnosis. We find no change in COVID-19 diagnoses among children under age 5, and the entirety of the effect is concentrated among children ages 5 to 18. For adult diagnoses, we find an overall increase of 0.2 per 10,000. However, the increase is concentrated among adults ages 19 to 29 and 30 to 39 (approximately 0.1 per 10,000 households increase for both).

These results are consistent with school reopenings leading to both between-household transmission to children, but also within-household transmission from children to adults (Chen et al., 2022; Paul et al., 2021). However, the direct effect of between household transmission (e.g., children infecting other children) is approximately three times larger than the indirect effect of within-household transmission (e.g., children infecting adult household members).

7.7. Differences for households with education workers

Additionally, an important consideration is the potential differential impact among teachers, administrators, and other school workers. To test for differences among education workers, we identify households in which the primary insurance subscriber works within the education sector. We are unable to account for households in which an education worker receives insurance coverage from a non-education family member. We are also unable to identify education worker job type and changes in mobility for the worker.

We estimate a similar model to Eq. (3) but interact county-level school visits with an indicator for the household receiving insurance coverage from an organization in the education sector. We do not find that households in which the primary insurance subscriber is employed by an educational organization are disproportionately likely to have a COVID-19 hospitalization, diagnosis after school reopening (Appendix Table A7).

7.8. Robustness test using alternative school closure data

Our main results use mobility tracking data to measure changes in foot traffic visits to schools. While used in many other studies, these data may imperfectly measure school reopening and closures. As an alternative approach, we use data from the COVID-19 School Data Hub on the percentage of school-year days in which each school district offered instruction that was fully in-person.³ These data have been frequently used to examine the effect of school closures (Halloran et al., 2021; Hansen et al., 2022; Bacher-Hicks et al., 2021; Halloran et al., 2023). To match our COVID-19 diagnoses data, we aggregate districts to counties. The School Data Hub data is also not week specific, so we aggregate COVID-19 infections across the study period. We do not use the School Data Hub data as our main source for identifying school closures due to its non-national coverage and potential data reporting inconsistencies.⁴

With these data, we use a similar empirical strategy, and compare COVID-19 infections based on the share of days in which a county’s schools are in-person. We also similarly compare infections rates between households with and without children. This comparison is descriptively presented in Appendix Figures A1 and A2, which compare the share of households with any COVID-19 hospitalization and COVID-19 infection, respectively, over the study period with the share of days in which schools are open in that county. For both outcomes, the results for households with children (Panel A) and without children (Panel B) are qualitatively similar. For both household types, the fit line indicates a noisy, but increasing correlation between in-person school and county-level infection rates. The results in Panel C present the county-specific differences in infection rates between households with and without children. This approach underlies our difference-in-differences empirical strategy. Consistent with our main results, we find an increasing relationship between the share of in-person school days and the difference in infection rates between households with and without children. These unadjusted differences suggest that moving from full remote to fully in-person leads to an approximately 50 per-10,000 household increase in cumulative infection rates.

8. Discussion

The COVID-19 pandemic upended all aspects of life. In response to concerns of COVID-19 infection, many schools shifted to remote instruction (Malkus and Christensen, 2020). However, the impacts of school reopenings on COVID-19 cases have not been well-estimated. In this study, we leverage variations in household composition and apply novel data on both COVID-19 diagnoses and county-level visits to schools to estimate the effects of school reopenings on COVID-19 transmission. We find that per 10,000 households, a one-log unit change in visits to schools leads to a 0.4 to 2.1 increase in COVID-19 cases. Our results further imply that moving from the 25th percentile of school reopenings to the 75th percentile translates to an approximately 3 % to 18 % increase in cases, depending on the specification. These results are robust to several specifications and after accounting for alternative policies that can impact COVID-19 transmission. In addition, we find that the modest increase in cases impacts both children and adults and does not differentially impact households with education-industry workers. Furthermore, in supplementary analyses we find that the increase in cases has little impact on medical spending. However, the effect is largest for households in lower-income counties, is larger during the peak of the COVID-19 pandemic and is concentrated in locations in the upper quartile of community transmission.

This study is not without limitations. For one, while broadly representative of the U.S. population with private insurance, we use a subset of the U.S. population. Importantly, our sample only includes those with employer-sponsored private insurance, and thus we do not include more economically vulnerable populations, such as uninsured individuals or those on public insurance, for whom the pandemic has a disproportionately larger impact. Our estimates likely underestimate the effects of school reopenings on more vulnerable populations. Likewise, we do not include individuals ages 65 and older, who are at increased risk to COVID-19. Our models do not account for changes in the education labor force that may impact the number of visits to schools. We do not include school-level mitigation measures that have been shown to impact COVID-19 transmission. Finally, the effects of school reopening on COVID-19 risk were estimated when COVID-19 vaccines were not available to teachers and the general population.

Despite these limitations, this study demonstrates that among the population we study, school reopenings lead to a small increase in COVID-19 cases. It is important to place these results in context with other risks of daily life and social distancing. While contributing to COVID-19 spread, in-person school also provides numerous benefits, as summarized above. For future pandemics, the key question for policymakers is the tradeoff between the costs of school reopenings and the costs of remote learning.

Supplementary Material

Supplementary material associated with this article can be found, in the online version, at doi:10.1016/j.jhealeco.2025.103025.