








key: cord-343414-2embihmf
authors: Wagner, Aaron B.; Hill, Elaine L.; Ryan, Sean E.; Sun, Ziteng; Deng, Grace; Bhadane, Sourbh; Martinez, Victor Hernandez; Wu, Peter; Li, Dongmei; Anand, Ajay; Acharya, Jayadev; Matteson, David S.
title: Social distancing merely stabilized COVID‐19 in the US
date: 2020-07-13
journal: Stat (Int Stat Inst)
DOI: 10.1002/sta4.302
sha: 
doc_id: 343414
cord_uid: 2embihmf

Social distancing measures have been imposed across the US in order to stem the spread of COVID‐19. We quantify the reduction in doubling rate, by state, that is associated with this intervention. Using the earlier of K‐12 school closures and restaurant closures, by state, to define the start of the intervention, and considering daily confirmed cases through April 23rd, 2020, we find that social distancing is associated with a statistically‐significant (p < 0.01) reduction in the doubling rate for all states except for Nebraska, North Dakota, and South Dakota, when controlling for false discovery, with the doubling rate averaged across the states falling from 0.302 (0.285, 0.320) days(‐1) to 0.010 (‐0.007, 0.028) days(‐1). However, we do not find that social distancing has made the spread subcritical. Instead, social distancing has merely stabilized the spread of the disease. We provide an illustration of our findings for each state, including estimates of the effective reproduction number, R, both with and without social distancing. We also discuss the policy implications of our findings.

We have used K-12 school (Education Week 2020) and restaurant (Wida 2020) closures as indicators of interventions. These were chosen because they represent the first widely-disruptive social distancing measures that were imposed. If a school closure was announced in the evening, we consider it as applying the next day. If closure was announced on a weekend, we used the first weekday for which schools were closed. The earlier of restaurant closing and school closing is defined as the intervention date for each state (Table B4) . Taking the earlier of the two reduces the likelihood of anticipatory behavior.

For the analysis in Appendix A on the confirmed case delay, we use data on COVID-19 cases by illness onset recorded by the (CDC 2020). We reference data on testing in New York State in Section 6. This data was obtained from the COVID Tracking Project (Covid Tracking Project 2020).

We focus on estimating the doubling rate, β, measured in inverse days, of new infections across the fifty states and the District of Columbia 1 , both before and after the intervention. We assume that during each period, the number of new infections per day is expressed as

where n is a discrete time index, α is a constant, and {Wn} is a mean-zero Gaussian noise process. The parameters α and β are assumed to vary both with the intervention and across states. Other than the change at the intervention, we assume that β is constant over time within a state.

This is tantamount to modeling the spread of the disease as a branching process (Athreya & Ney 1972) , which is appropriate if the time horizon is sufficiently short that the fraction of susceptible individuals is approximately constant. When working with branching-process models of infectious diseases, it is common to consider the expected number of new infections caused by a single infected individual; in epidemiology this is called the effective reproduction number, R. If R > 1, then the number of infected individual grows exponentially and we say the process is supercritical. If R < 1, it contracts exponentially, and we say the process is subcritical. If R = 1, we call the process critical. One can compute R from the doubling rate β and the distribution of the serial interval using the Lotka-Euler equation (Dublin & Lotka 1920; Feller 1941) . For any serial interval distribution, this transformation maps positive β values to superunity R values and negative β values to subunity R values. We focus on the doubling rate, rather than R, because it can be more directly estimated from the time-series of confirmed cases and because it is more useful for making short-term predictions about confirmed case counts and hospital loads. One can obtain a simple upper bound on R in terms of β and the mean serial interval µ by applying Jensen's inequality to the Lotka-Euler equation (Wallinga & Lipsitch 2007) ,

Prior work has estimated µ at 4 days for COVID-19 (Du et al. 2020; Nishiura., Lintona, & Akhmetzhanova 2020) . All of the doubling-rate estimates in this paper can be translated to estimated upper bounds on R using this inequality, although the resulting bounds are less certain than the underlying estimates of β due to the exponentiation and uncertainty about µ. 2

Considering each state in isolation, we estimate the doubling rate before and after the intervention as follows. Let Cn denote the number of new confirmed cases on day n, where the index n = 1 refers to the first day after March 1st for which the state records at least two consecutive days of positive confirmed cases. This convention is designed to appropriately handle states with one very early case (e.g., Washington) followed by many days of zero cases. We model Cn as proportional to a delayed version of the quantity in (1):

where 0 < θ ≤ represents the fraction of newly infected people that are confirmed to have the disease; note that θ can be absorbed into α for the purposes of modeling Cn. We apply the transformation

Including the effect of the intervention (but ignoring the effect of the add-one transformation to Cn), we model {Yn} as

where 1(·) is the standard indicator function, and {Wn} satisfies

where {Zn} is an independent and identically distributed (i.i.d.) Gaussian sequence with mean zero and variance σ 2 , making {Wn} a first-order autoregressive [AR(1)] Gaussian process. The parameter d represents the state-specific intervention date defined in the previous section. Thus d is known but state-dependent. The quantity N, which we call the confirmed case delay, represents the average time (in days) between when someone is infected with SARS-CoV-2 and when they are confirmed to have COVID-19 and included in the published counts. We assume that N is integervalued. The parameters β 0 and β 1 are the doubling rates before and after, respectively, the intervention. The unknown parameters in the model are α, β 0 , β 1 , N, γ, σ 2 .

We are particularly interested in β 0 , β 1 , and N.

For each of the states, we fit the model using two approaches, which differ primarily in how they handle the confirmed case delay, N. The first, which we call the learned-delay approach, fits N to the data on par with the other parameters in the model. This is tantamount to finding a changepoint in the {Yn} time-series for which there is a significant difference between the doubling rates. The difference between the changepoint epoch and d then forms a point estimate of N. For this purpose, we use an algorithm that declines to identify a changepoint (effectively setting (Fearnhead, Maidstone, & Letchford 2019) . For states with a detected changepoint, we then obtain a point estimate of N in addition to the other parameters, which can vary by state. This approach assumes γ = 0, so that the errors are taken to be i.i.d.

The second approach, which we call fixed-delay, takes the confirmed case delay to be N = 12 for all states. This choice can be justified as follows.

First, 11.5 is the median estimate of N across the states obtained by the learned-delay method (See Fig. 3 ). Second, estimating the confirmed case delay from a separate analysis of CDC data gives a point estimate 12 days, as described in Appendix A. The fixed-delay method does not require that γ = 0, i.e., it allows for {Wn} to be AR(1). For both methods, the unknown parameters are estimated via maximum likelihood. The code for both methods is available, along with copies of the datasets used and the scripts needed to produce the figures in the paper (Wagner et al. 2020 ).

Tables B1 and B2 in Appendix B show the results of the learned-delay model and fixed-delay model, respectively. Fig. 6 compiles all of the findings from both models. Table B1 includes estimates of the confirmed case delay, N, for those states for which a changepoint is detected by the learned-delay model.

This column of the table is plotted in Fig. 2 , and a histogram is provided in Fig. 3 . The median is 11.5 days, which supports the choice used in the fixed-delay model, as noted earlier. The model declines to declare a changepoint for three states, whose standard plot is shown Fig. 4 . For such states, this model does not find evidence of the efficacy of the social distancing measures imposed. For Nebraska in particular, the intervention occurred quite late (Apr. 3rd), so it is possible that the change is simply not observed in the available data. It should also be noted that these states had some of the lowest pre-intervention doubling rates, according to Fig. 6 .

Standard plots (showing the fitted learned-delay model) for each state are provided in Figs. B1-B4 in Appendix B. As exemplars, we consider three states that were among the first in the US to have confirmed cases, namely New York, California, and Washington. These states have large numbers of confirmed cases, making the data from these states of higher quality. Since the number of deaths is at least an order of magnitude lower than the number of cases, for most states the former is too noisy to be of much use. For these states, however, it provides a useful comparison with the confirmed case counts.

The results of our analysis for these three states is shown in Fig. 5 . For all three states, we see two regimes for the growth rate for both the confirmed cases and deaths data. The growth rate begins in a supercritical state indicating exponential growth. The growth rate then decreases substantially, presumably indicating that the intervention is making an impact, albeit with a delayed effect. However, we note that the number of confirmed cases and deaths does not rapidly decline after the change for California and New York, whereas the Washington plot appears to show a decrease in both cases and deaths as a result of the intervention.

To determine the significance level of this finding, we turn to the fixed-delay model, which provides approximate 95% confidence intervals for the doubling rates and their difference (see Table B2 ) using the Student's t distribution to account for the small sample size. It also provides approximate p-values against the null hypotheses that β 1 ≥ 0, β 0 ≤ 0, and β 1 ≥ β 0 . We utilize a one-sided t-test for both cases, with a significance level of 0.05.

A one-sided test is appropriate since we hypothesize the pre-intervention period should show signs of rapid growth in the number of cases, and after the intervention, there should be a significant decrease in the doubling rate. We find that the intervention is associated with a statisticallysignificant decrease in the doubling rate (p < 0.01) for all states, even after controlling for false discovery rates using the Benjamini-Hochberg procedure (Benjamini & Hochberg 1995) , except for Nebraska, South Dakota, and North Dakota. When controlling for false discovery, we are not

able to conclude that any of the states have achieved a negative β 1 ; Washington comes the closest with respect to statistical significance. Recall that Nebraska, South Dakota, and North Dakota are also the states for which the learned-delay method does not find a significant changepoint.

The point estimates across the ensemble of states also show a substantial reduction in the doubling rate associated with the intervention, with the post-intervention doubling rate being close to critical. The pre-intervention doubling-rate averaged across all states is 0.302 (0.285, 0.320) days −1 . Post-intervention, it is 0.010 (−0.007, 0.028) days −1 , the difference being −0.292 (−0.296, −0.288) days −1 . Using Eq.

(2), these estimates translate to estimated upper bounds on R pre-and post-intervention of 2.310 and 1.028, respectively, or a 55% reduction in contact between contagious and susceptible individuals. It should be emphasized, however, that there is a considerable variation in these values among the states, and the R induced from the average doubling rate is distinct from the average of the induced R values. Estimated bounds on R for each state are provided in Table B3 and Fig. 7 .

Thus while this study finds social distancing measures to be effective at reducing the spread of SARS-CoV-2, it does not find conclusive evidence that they have pushed the spread into the subcritical (β 1 < 0) regime. Across the ensemble of states, the post-intervention slopes are in fact quite close to zero. The mean slope of the point estimates is 0.010 days −1 , as noted earlier, with 31 of the states having a post-intervention doubling rate between −0.05 and 0.05 days −1 , which corresponds to a doubling or halving time exceeding twenty days. This indicates that the pandemic across many regions plateaued, rather than contracted, post-intervention, with each infected individual infecting nearly one other individual on average (R = 1). In those locations, COVID-19 under social distancing provides a naturally-occurring example of a near-critical branching process (Athreya & Ney 1972) , and the observed plateau should be contrasted with the symmetrical apex that is presumed in some predictive models (IHME COVID-19 health service utilization forecasting team 2020).

For the fixed-delay method, we conducted a sensitivity analysis on the order of the autoregressive noise process and found that allowing for higher-order dependence did not significantly improve the fit. For each state, we conducted a Ljung-Box test for up to 7 lags on the residuals of our fixed-delay model, and after adjusting for multiple testing using an FDR procedure (Benjamini & Hochberg 1995) , none of the states showed evidence of higher-order autocorrelation. We also tested for residual normality using Kolmogorov-Smirnov test, and also found that after adjusting for multiple testing, none of the states showed statistically-significant deviations from normality.

This study finds that the social distancing measures enacted in the US are associated with a significant decrease in the doubling rate of COVID-19 infections. Indeed, the exponential growth that was observed pre-intervention was stabilized with the intervention. The study thus provides support for the use of social distancing measures. The study also points to the importance of timeliness when imposing such measures. Roughly speaking, the number of daily new cases was doubling every three days pre-intervention, and became constant with the intervention. As such, we expect that intervening just three days earlier would have halved the number of daily new cases post-intervention.

Given the substantial social and economic costs of such measures, there is interest in the question of when they should be relaxed. As of late April, some states have already begun this process with Georgia allowing certain businesses, such as gyms and barbershops, to reopen (Hagemann & Booker 2020). In fact, Alabama, Florida, Georgia, Mississippi, South Carolina and Tennessee announced a coordinated attempt to reopen (Dixon 2020; McArdle 2020) . Standard plots for these states are shown in Fig. 8 .

Since a systematic relaxation of social distancing will presumably increase the doubling rate, from a public health perspective it is advisable to relax such measures only when there is evidence that the spread has become subcritical. Among negative doubling rates, those that are farther from zero (i.e., are larger in absolute value) allow for more relaxation of social distancing measures without the spread returning to supercriticality.

We see that the curves for these states appear similar to those for the early states in Fig. 5 . In particular, we see a substantial change in the growth rate occurring some days after the intervention, but the spread does not appear to have become subcritical, with the exception of South

Carolina and possibly Florida. This study finds that other states, such as Idaho, Vermont, Montana, Washington, and Hawaii have a stronger basis for relaxing social distancing at this time.

The lack of clear subcriticality among the post-intervention doubling rates suggests that existing social distancing measures will need to remain in place for some time. On the other hand, it is possible that a subset of the existing social distancing measures are responsible for the observed reductions in the doubling rate. If this is the case, then the remaining measures could be relaxed with no harmful effect. Also, any additional measures taken, such as contract tracing or the use of masks, will tend to reduce the doubling rate further. Finally, in the absence of a change in interventions, the doubling rate will tend to decrease over time as the population of susceptible individuals decreases. 

Our analysis relies on the number of confirmed cases of COVID-19 reported by federal, state, territorial, and local authorities. Beyond the delay between infection and confirmation, which was discussed earlier, this statistic likely underestimates the number of actual cases, and it could be subject to selection bias. We note, however, that if the confirmed case counts reflect a constant fraction θ of the actual number of cases, as assumed in our model, then this undercount will not materially affect the estimation of the doubling rate β since θ · Cn and Cn grow at the same exponential rate. Likewise, the doubling rates in different subpopulations cannot diverge so long as those subpopulations are sufficiently connected, making sampling bias less of a concern.

Of greater concern is variability in the availability of tests, as temporal variation in testing could affect the estimates of the doubling rate. New York State, for instance, saw a rapid increase in the number of daily tests followed by a plateauing around March 19th, as shown in Fig. 9 . This approximately coincides with the detected changepoint in the number of confirmed cases by the learned-delay method. It is possible that for some states, the abrupt change that we detect in confirmed cases does not reflect an actual change in the spread of disease but only a change in detection capabilities.

Controlling for this effect is challenging because the data on the number of tests is subject to additional types of errors. States vary in whether their test counts report the number of distinct people tested or the number of tests performed, and whether they represent the number of tests taken or completed. Data on the number of tests is also not available for all of the states for the time interval considered here, as some states initially reported only confirmed cases.

One could potentially rely on the number of deaths attributed to COVID-19 instead of the number of confirmed cases. This approach is subject to four complications, however. First, the mean time between infection and death is presumably longer than the time between infection and Mitigating this concern, we note that for New York, the number of tests plateaued slightly before the number of cases did. We also note that data on deaths and hospitalizations, while lower in quality than the number of confirmed cases, are broadly consistent with the findings based on the confirmed case count alone. Notably, we do not see pronounced increases or decreases in deaths or hospitalizations post-intervention for states in which the estimated doubling rate post-intervention is near zero. We also do not see a saturation in the fraction of positive tests, which would indicate an uncaptured exponential increase in the number of actual COVID-19 patients. Finally, several states have continued to see supercritical growth post-intervention.

Another limitation of our analysis is that it treats states separately and thereby ignores the influence that neighboring states have on one another. Nor does it capitalize on the potential similarity among the model parameters for similar states. We also assume an unchanging reservoir of susceptible individuals; an SIR-type model (e.g., Martcheva (2015) ) is appropriate when the fraction of the population that is exposed to the virus varies over the period under study. Our analysis assumes a single changepoint when the first large-scale social distancing measures are imposed. It cannot distinguish among the relative benefits of different interventions imposed around the same time. It also does not account for anticipatory behavioral changes that could have preceded the formal imposition of interventions. Several factors, for which this study does not control, could have contributed to differing doubling rates between the pre-and post-intervention periods, separate from the social distancing measures considered here. These include improvements in treatment, changes in the weather, and the adoption of mask-wearing. An analysis that controls for these effects would be valuable, as would one that used mobility data instead of state policies as the input. Subsequent analyses may require additional changepoints as states relax, and possibly reimpose, social distancing measures, however. The confirmed case delay could also vary over time as a result of changing testing protocols.

The data that support the findings of this study are openly available from the New York 

The quantity N is the sum of the mean incubation time and the mean time between symptom onset and confirmed diagnosis. Various works have estimated the mean incubation time to be 5 days (Backer, Klinkenberg, & Wallinga 2020; Lauer et al. 2020; Li et al. 2020) . We focus here on estimating the time between symptom onset and confirmed diagnosis.

We estimate this quantity using data from the CDC (CDC 2020). The CDC reports COVID-19 cases in the United States by date of illness onset from January 12, 2020, to April 15, 2020, as well as by date of confirmed diagnosis (Fig. A1, top) . The CDC warns that estimates are not accurate after April 5, 2020 due to difficulty in accurately determining illness onset after community spread began.

We truncate the time-series so that both end when their respective cumulative counts reach 10,000 (Fig. A1, middle) . The lag between illness onset and case confirmation is determined using a normalized cross-correlation operation (Fig. A1, bottom) . The lag is estimated to be 7 days.

When added to the incubation time, this results in a total time of 12 days from exposure to confirmed test, which essentially coincides with the estimate of 11.5 days obtained in the body of the paper. An earlier work estimated the mean time from symptom onset to confirmed test to be 4.8

days (Pellis et al. 2020) , which translates to a point estimate of N of about 10 days. 

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