Suffering in silence: How COVID-19 school closures inhibit the reporting of child maltreatment

Abstract

To combat the spread of COVID-19, many primary and secondary schools in the United States canceled classes and moved instruction online. This study examines an unexplored consequence of COVID-19 school closures: the broken link between child maltreatment victims and the number one source of reported maltreatment allegations-school personnel. Using current, county-level data from Florida, we estimate a counterfactual distribution of child maltreatment allegations for March and April 2020, the first two months in which Florida schools closed. While one would expect the financial, mental, and physical stress due to COVID-19 to result in additional child maltreatment cases, we find that the actual number of reported allegations was approximately 15,000 lower (27%) than expected for these two months. We leverage a detailed dataset of school district staffing and spending to show that the observed decline in allegations was largely driven by school closures. Finally, we discuss policy implications of our findings for the debate surrounding school reopenings and suggest a number of responses that may mitigate this hidden cost of school closures.

Keywords: COVID-19; Child maltreatment; School closures.

Graphical abstract

Fig. 1

Time series of the number of allegations in Florida. Notes: The figure shows the time series of allegations received by the Florida Child Abuse Hotline from January 2015 to April 2020. The grey shaded regions highlight months when school is not in session (June, July, and December), while the red circles highlight the months of March and April. Data on child abuse allegations come from the Florida DCF.

Fig. 2

Actual vs counterfactual number of allegations. Notes: The figure shows the difference between the actual and predicted counterfactual number of allegations for each month of the 2019–20 academic year and separately for the total number of allegations (Panel (a)) and for the total number of accepted allegations (Panel (b)). The counterfactual number of allegations comes from estimating Eq. (1) excluding January, February, March, and April 2020 and specifying f( ⋅ ) as a third-order polynomial.

Fig. 3

Additional specifications. Notes: Panels (a) and (b) show the estimated $\widehat{\theta }$'s, along with 95% confidence intervals by month. Standard errors used in the construction of the confidence intervals were two-way clustered at the county and month levels. The $\widehat{\theta }$'s come from estimating nine separate variants of Eq. (2) where we replace the SchoolClosures_my dummy variable with an indicator variable equal to one for an alternative month in the 2019–20 academic year. Panel (a) shows the results obtained when using the total number of allegations as the dependent variable, while Panel (b) shows the results for allegations accepted for investigation. Panels (c) and (d) show the empirical cumulative distribution function of the placebo estimates (as blue dots), as well as the actual estimated $\widehat{\theta }$ from Eq. (2) (as a red diamond), separately for the total number of allegations and allegations accepted for investigation, respectively. The placebo estimates are obtained by estimating variants of Eq. (2) where the SchoolClosures_my dummy variable is replaced with an alternative month-year indicator from the permutation of all month-year combinations between January 2004 and December 2019. This yields a distribution of $\widehat{\theta }$ based on 192 placebo estimates of θ (12 months × 16 years).

Fig. 4

Heterogeneity by school district characteristics. Notes: The figure plots estimates of δ from the estimation of Eq. (3), along with 95% confidence intervals. Standard errors used in the construction of the confidence intervals were two-way clustered at the county and month levels. Panel (a) presents estimates of δ from five separate regressions, each exploring heterogeneity by a specific staff-student ratio. Panel (b) presents estimates of δ from five additional regressions, each exploring heterogeneity by a specific expenditure account.

Fig. A.1

State deviations from the national average. Notes: The figure shows absolute deviations from the national average in the number of allegations per 1000 children (Panel (a)) and the share of allegations accepted for investigation (Panel (b)) by state. The solid black bar represents the state of Florida. Unfilled bars represent the remaining states in the contiguous U.S., with the exception of Illinois, New Jersey, New York, North Carolina, North Dakota, and Pennsylvania, for which these data were unavailable. Data on each state's child maltreatment allegations come from the 2018 Child Maltreatment Report (Administration for Children and Families, 2020).

Fig. A.2

Alternative definitions of local months. Notes: The figure shows the difference between the actual and predicted counterfactual number of accepted allegations for each month of the 2019–20 academic year. The counterfactual number of accepted allegations comes from estimating Eq. (1) and specifying f( ⋅ ) as a third-order polynomial. Panel (a) shows our baseline specification which excludes the months of January, February, March, and April 2020 when estimating Eq. (1). Panels (b), (c), and (d) display the results obtained when instead excluding only February, March, and April 2020; March and April 2020; and all available months in the 2019–20 academic year, respectively.

Fig. A.3

Actual vs. counterfactual (linear and quadratic). Notes: The figure shows the difference between the actual and predicted counterfactual number of allegations for each month of the 2019–20 academic year and separately for the total number of allegations and for the total number of allegations accepted for investigation. The counterfactual number of allegations comes from estimating Eq. (1) excluding January, February, March, and April 2020. Panels (a) and (b) display the results obtained when specifying f( ⋅ ) as a first-order polynomial, while Panels (c) and (d) show the results when specifying f( ⋅ ) as a second-order polynomial instead.

Fig. A.4

Alternative standard error specifications. Notes: The figure shows re-estimation of the results presented in Panel (b) of Fig. 3. Panel (a) displays the baseline estimates in which standard errors used in the construction of the 95% confidence intervals were two-way clustered at the county and month levels. Panels (b) and (c) show the estimates obtained when clustering standard errors at the county and month levels, respectively.