Main analysis

On March 11^th 2020, the Italian Prime Minister mandated to shut down all food, retail and personal-services activities. Businesses such as supermarkets, small grocery shops, pharmacies, and newsstand kiosks were allowed to remain open. The national decree also introduced restrictions on personal mobility. Two weeks later, on March 25^th, the list of sectors included in the shutdown policy was enlarged.

For reasons of identification, our study primarily focuses on the first policy. We study the impact of this shutdown on mortality rates using a difference-in-differences (hereafter diff-in-diff) approach with continuous treatment. Given the lag between a virus infection and a (possible) subsequent death, the “treatment” date does not coincide with the day the policy was enacted. It is impossible for the policy to have any effect on mortality from its implementation date. Estimates in the literature suggest a median of five days between exposure to the virus and the occurrence of first symptoms [18] and about eight days between first symptoms and death [19]. Thus, the median time to death across individuals is about 13 days. Due to variation around this mean, any effective policy will arguably produce its effects two or three days before this date; we therefore take the “treatment date” to be day 10.

Our empirical model takes the following form: (1) where y_m,t is the (Covid-related) mortality rate in municipality m on day t. We include the lagged value, y_m,t−1, as a determinant since epidemiological models (such as the SIR model, [20, 21]) show that new infections condition highly on the prevalent share of infected people in the population. We include two dummies, d11_t and d25_t, to indicate the treatment date for the first and second shutdown, both taking value of one as of the tenth day after their respective announcements. The variables Shutdown11_m and Shutdown25_m measure the exposure of a municipality to sectors that were incrementally shut down at the first and second shutdown, respectively. Our variable of interest is the interaction coefficient ϕ, which captures whether municipalities with a higher shutdown exposure experience lower daily mortality rates as a consequence of the policy. If the policy shutdown is effective at reducing the spread of the virus, and thus ultimately reduces mortality, then the prediction is that the coefficient ϕ will enter with a negative sign. We saturate the model with municipality and day-fixed effects as well as with proxies for a municipality’s stage in the pandemic (tsa; to be explained below). Lastly, we include interactions of municipality-level variables with the policy dummy d11_t to control for heterogeneous patterns across municipalities following the policy that are unrelated to business shutdown exposures (e.g., due to confounding policies).

We next describe the calculation of the variables. We construct measures of shutdown exposure using granular data on employment and establishments of Italian firms made available by the Italian Statistical Agency (ISTAT). The dataset provides sectoral data at the municipality-level from the year 2017 [22], including information on the number of employees and business owners, revenues and number of establishments. We construct a continuous municipality-level shutdown exposure Shutdown11_m by dividing the number of employees and business owners in sectors shut down on March 11^th by the total number of all employees and business owners in the municipality. Shutdown sectors correspond to the following European classification of the economic activities (NACE) codes: “451”, “452”, “473”, “474”, “477”, “478” for the retail industry; “561”, “563” for the food and beverages industry; “96” for the personal-services industry. We exclude employment in schooling and sports (NACE codes “85” and “931”) from the denominator, since these sectors were already shut down weeks before. Additionally, we exclude from the sample the eleven municipalities in northern Italy that were quarantined as “red zone”, since the shutdown policies we focus on do not apply there. We construct an equivalent measure of the second shutdown, Shutdown25_m, using the employment ratio of sectors that were incrementally shut down on the 25^th.

We next describe our measure of policy effectiveness, which is based on Covid-19 deaths per 100,000 inhabitants. In early June 2020, ISTAT released death registry data for 7,272 Italian municipalities (covering more than 93% of the entire population, see [23]). The dataset contains the number of deaths per day, along with the residence location, gender, and age bracket of the deceased, over the first quarter of 2020. Using mortality rates offers several advantages. First, alternative measures of Covid-19 related outcomes based on infections or hospital admissions suffer from biases. For example, a higher Covid-19 test intensity will inevitably show higher infection rates. In addition, in regions with worse healthcare conditions and low proximity of hospitals, the usage of hospitals per capita was (mechanically) lower. Many deceased people who had shown no or mild symptoms (asymptomatics) were simply not accounted in the official Covid-19 statistics because they were not hospitalized (e.g., due to the limited capacity of hospitals). Second, the collection process for death registry records minimizes reporting lags and subjectivity in recording information (e.g., residence at time of death). [24] show there was also significant underreporting of official Covid-19 deaths in Italy. Third, deaths also capture mortality cases that are indirectly attributable to Covid-19. For example, evidence suggests that mortality resulting from heart attacks more than tripled during the pandemic in Italy [25], likely because of hospital congestion or the unavailability of ambulances.

A disadvantage of the death registry data, though, is the information missing on the cause of death. We therefore use a statistical method to infer deaths related to Covid-19, based on deviations from historical patterns. Specifically, we calculate excess mortality, i.e., attributable to Covid-19, by deducting from a municipality’s (daily) number of deaths the average number of deaths over the previous five years in the same municipality, using an evenly-spaced-around window of seven days. We scale excess deaths by the population to arrive at the following measure: (2)

There is an important source of heterogeneity across municipalities: the virus reached different municipalities at different points in time. Failing to address this heterogeneity is likely to lead to an inappropriate econometric specification. In particular, a municipality that was hit early by the virus might likely display lower growth in contagion (as the curve has already levelled off) compared to a region with low virus intensity. Due to the highly non-linear dynamics of a pandemic, municipality-level fixed effects might not appropriately account for such heterogeneity. In our empirical analysis, we therefore account in our empirical analysis for the “time of arrival” of the virus to compare municipalities that are at the same stage of the pandemic. We classify the time of arrival in a municipality based on two criteria: “anomaly” and “persistence”. The former is measured by the day in which the cumulative excess deaths in a municipality surpass one standard deviation of its distribution over the first four months of 2020. For the latter criterion we require that the cumulative mortality rate among residents of a municipality m reaches a threshold of 100 deaths per 100,000 inhabitants at some point during the same sample period. We classify the time of arrival of a virus as the day when the first criterion is met for a municipality that fulfils the second criterion (which is time-invariant). We have visually inspected our classifications for a number of municipalities, and have found them to be reasonable. Studying the econometric properties, we find the arrival day of the virus lies in between the first and second structural break of a municipality’s cumulative mortality rate time series.

Note that according to our definition, some municipalities were not subjected to the virus during the first four months of 2020 (about 500 municipalities). We exclude these from our main dataset, but use them later in a placebo test. To limit noise in our measure of Covid-19 deaths per capita, we also require a municipality to have at least 4,500 inhabitants. This leaves us with 2,145 municipalities, spanning 105 provinces and 20 regions. The sample covers the period from February 22^nd to April 13^th.

Table 1 provides the summary statistics of our sample. The mean across time and municipalities of the variable ExcDeathRate_m,t is about 4. That is, there are on average four Covid-related deaths a day per 100,000 inhabitants. The average exposure to the first shutdown, Shutdown11_m, is about 17.6%, whereas the average exposure to the second policy, Shutdown25_m is larger (32.4%). There is also sizable cross-sectional variation in the exposure to both policies. As explained, we will focus mostly on the first shutdown; the impact of the second shutdown might be partly confounded by the first one and hence offers a less clean setting. The table also contains information on the breakdown of sectors closed on the March 11^th. We can see that both the food and beverage sector and the retail sector on average are about 7%, whereas the personal services sector is smaller (less than 3%).

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Table 1. Summary statistics.

https://doi.org/10.1371/journal.pone.0251373.t001

The table also lists several other variables that are used in the analysis. To control for heterogeneity in characteristics that affect transmission, virulence, or the ability to comply with movement restrictions, we collect data on population density (PopDensity_m), education (HighSchool_p), income inequality (IncIneq_m), age structure (Elderly_p), and the degree of internal commuting (IntMob_m). The Hospit_p variable is the hospital capacity in a province p, measured as the sum of the number of beds available in hospitals, as a fraction of the total population (source: Ministry of Health). To study spillovers, we include information on the shutdown exposures of the largest business centre of the province where the municipality is located. Among the province’s larger municipalities (with at least 16,500 inhabitants), we identify the business centre in three alternative ways: as the municipality with the highest relative share of closed sectors, RelShutdown11_n; the average shutdown exposure of these municipalities under this method is 23.73%, which is by construction larger than the unconditional mean; next, as the one with the highest absolute number of employees and business owners in the shut down sectors, AbsShutdown11_n; finally as the one with the largest population, PopShutdown11_n. Next, the variable WinterTourists_p measures tourist intensity in a province. It is calculated as (foreign) tourists visits during January and February, scaled by population [26]. The top-10 provinces according to our tourist proxy contains skiing provinces (e.g., Trento, Bolzano, Sondrio) and historical cities (e.g., Florence, Venice, Rome). The WeekArrival_m variable is the number of weeks that elapsed between the arrival of the virus (calculated as described above) and the effective date of the first policy (March 21^st). We can see that, on average, a municipality starts experiencing the virus for the first time in early February, about one month before the effective date of the first policy. Lastly, DaysArrival_m,t measures the time elapsed from the day on which the pandemic begins in a municipality m. A comprehensive definition of the variables can be found in S1 Table.

Robustness

Table 4 contains the estimation results from various modifications of our baseline specification (the last column of Table 3).

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Table 4. Robustness tests.

https://doi.org/10.1371/journal.pone.0251373.t004

Our analysis has shown that high and low exposure municipalities do not display differences in the outcome variable (both in terms of level and trend) prior to the effective date. Thus, the standard parallel-trend assumption on which identification in diff-in-diff models relies is met. However, a potential concern is that municipalities with different shutdown exposures might also differ among other dimensions, and that this might create heterogeneous responses to confounding effects around the effective date. To some extent, we alleviate such concerns by including interaction terms of the post treatment date dummy d₁₁ and important municipality-level characteristics (in columns 3, 4, and 5 of Table 3). In addition, we perform an analysis in which we match “treated” (above median exposure) to “control” municipalities (below median exposure). Using a two-step propensity score-matching algorithm, we first match on the week of virus arrival and subsequently on the three characteristics that showed up significantly in Table 2 (population density, income inequality, and mobility). We match each treated municipality to a control with replacement, and discard treated municipalities for which no good match is available. This procedure yields in total 873 treated and 444 control municipalities. As expected, there are no longer significant differences between the treatment and control sample when we perform the balance variables test of Table 2 on the matched sample (results available on request). Fig 3 presents the propensity score-matched equivalent of Fig 1, and show a graph very similar to the one in Fig 1.

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Fig 3. Mortality rates in high and low shutdown matched municipalities.

2-step propensity score matched (first on virus arrival week and then on PopDensm, IntMobm and IncIneqm) municipalities’ average within-group excess mortality rates over time. Vertical lines identify the first announcement (τ = 0 corresponds to 03/11) and treatment date (τ = 10 to 03/21). A group excess mortality rate is calculated by averaging values across treated municipalities (above the median Shutdown11m, N = 873) and across control municipalities (those below the median, N = 444). Blue line: HighShutdown. Red line: LowShutdown.

https://doi.org/10.1371/journal.pone.0251373.g003

The first column of Table 4 shows the baseline results (equivalent to column (5) of Table 3) for the matched sample. The coefficient of interest is smaller (in absolute terms) but of similar magnitude as in the baseline model (−0.03 versus −0.0358).

Another concern with our analysis is that our results might be driven by specific municipalities, such as the ones in the epicentre of the outbreak in Lombardy or winter tourism hotspots. To investigate this, we focus on subsamples from which we exclude municipalities in Lombardy (column (2)) and winter tourist regions (column (3)). Results are similar to our baseline specification in column (5) of Table 3.

In column (4), we shorten the post-treatment period to April 4^th, that is, before the treatment date for the second policy. This avoids any confounding effect stemming from the second shutdown. The coefficient of interest remains at a similar level.

We also assess the robustness of our baseline result to a more restrictive classification of the virus arrival time. In particular, we identify the onset of the pandemic in a municipality m when the cumulative mortality rate surpasses two (rather than one) standard deviations of its distribution. Column (5) shows that the coefficients on the interaction terms of both policies are very similar compared to the baseline estimates. The results are also robust to changing the “anomaly” threshold to the first decile of each municipality cumulative deaths distribution (results available upon request).

Our main model specification in Eq (1) includes a lagged dependent variable, which is consistent with the idea that new infections (and resulting new deaths) condition highly on prevailing infections (and hence recent excess mortality). However, the inclusion of a lagged-dependent variable in OLS regressions creates an econometric problem in small samples, by causing a downward bias in the estimation of the coefficient on the lagged-dependent variable [29]. To rule out any issues resulting from such a bias, we first exclude the lagged dependent variable in column (6). Moreover, in column (7), we estimate a system GMM as in [15], instrumenting the variables in levels with their first differences. We optimally collapse the number of instruments and, to correct for the finite sample standard errors, use a two-step procedure [30]. Both specifications give similar or even stronger results than our baseline specification. Fig 2 confirms this, showing an average point estimate of lives saved exceeding 12,500 over a period of 24 days using the system GMM.

Finally, we consider three falsification tests. First, we move the first policy treatment date to 10 days earlier (column (8)), terminating the sample period at March 20^th. In column (9) we cross-interact time dummies and sectoral exposures, that is, we run the regression with d25_t × Shutd11_m and d11_t × Shutd25_m. Third, we run the regression for the 477 municipalities in which the virus never circulated at any point during our sample according to our statistical methodology (column (10)). In all placebo tests, the coefficient on the policy interaction term shrinks substantially in size and becomes statistically insignificant.

Contagion channels

Table 5 further explores the mechanisms behind our baseline results (column (5) of Table 3).

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Table 5. Contagion channels.

https://doi.org/10.1371/journal.pone.0251373.t005

In column (1) we focus on mortality rates of people older than 65 years, that is, among a group that is unlikely to work. Thereby, we effectively exclude employees and business owners from the sample. Column (1) shows that the results – although a bit weaker—are very similar to our baseline specification. We obtain comparable results (unreported) when we focus on people with an age above 80, in which case direct involvement in business activities becomes very unlikely. These results point to a contagion externality from business activities [2], which is an important result from a policy perspective. If people within a firm were predominantly infected, standard economic theory would suggest less of a need for policy interventions as any utility loss due to contagion is then more likely to be internalized (in particular, workers might require higher wages to keep working during the pandemic, or simply stop turning up at work). However, if production also considerably affects mortality rates outside the firm, decentralized production decisions are likely to be sub-optimal, necessitating policy interventions.

Next, column (2) explores the role of hospital capacity. We would expect policies to be more effective in reducing mortality rates in areas with congested hospitals (as virus contagion is then more likely to be fatal). Consistent with this conjecture, we find the triple interaction coefficient of hospital capacity, the first policy exposure, and the post-treatment dummy to be positive and significant.

So far we have examined the impact of the policy exposure on mortality rates in the municipality itself. However, larger and more developed cities also attract workers from other municipalities. We might therefore expect business shutdowns in large and/or interconnected municipalities to have positive spillovers on other municipalities. To investigate this hypothesis, we also include in our baseline model an interaction effect of the largest exposed municipality in a province (column (3)). In line with the idea that cities with a high sector concentration attract people from neighbouring municipalities, the coefficient on the interaction between Shutdown11_n and the first shutdown date is negative and significant. Interestingly, it is similar in magnitude as the main within-municipality effect. Similarly, we find statistically significant negative coefficients under two alternative measures: the municipality with the largest absolute number of employees in the shut down sectors (column 4) and with the largest number of inhabitants (column 5). All in all, this points to important spillovers from shutdowns across jurisdictions. [5] show that such cross-jurisdictional spillovers make uncoordinated lockdown decisions inefficient, and derive implications for international cooperation of lockdown policies. Our evidence suggests that coordination among units or centralization of containment policies might be required to achieve optimal containment policies. Fig 2 (last bar) shows that, taking (relative) spillovers into account, the economic effect increases to over 16,000 lives saved.

We also examine whether policy effectiveness exhibits decreasing or increasing returns to scale. First, we include an interaction term with squared shutdown exposure (column (6)). This squared term shows up significantly positive, indicating decreasing returns to scale for business shutdowns. Second, we sort municipalities within each province into terciles according to their exposure to the first policy, and then run a regression interacting our variable of interest with each Shutdown11_m tercile dummy (column (7)). Comparing the coefficients on the shutdown exposure across the different terciles we see that they are consistently declining (in absolute terms) as we move from low to high shutdown exposures. Once again, a marginal unit of shutdown matters less in municipalities with higher shutdown exposure. These results suggest there are declining returns to shutting down businesses. This evidence is consistent with the non-linear nature of epidemiological dynamics. In particular, once the virus is sufficiently contained, the marginal benefit of reducing the reproduction rate further declines. An alternative explanation for the declining coefficients is that a high exposure municipality might also be the largest exposed municipality of the province, in which case the coefficient estimate underestimates the total effect due to the spillovers (as shown previously). However, we still obtain declining coefficients once the largest exposed municipalities are dropped from the sample (results available upon request). In column (8), we formally check whether the declining marginal returns result partially explains the low effectiveness of the second shutdown policy. If shutting down a large part of the economy has already contained the virus, additional shutdowns (on the same day, or two weeks later) matter less. Noticeably, including only the first two Shutdown11_m terciles in the sample, the d25_t × Shutdown25_m coefficient becomes significant (at 95% level). Therefore, the second shutdown is effective in the low first shutdown exposure sample and hence, our result of a lower effectiveness of the second shutdown is driven by decreasing returns to scale.

The last column of the table decomposes the first shutdown exposure into different sectors. We create exposure variables for all three sectors (food, retail, and personal services) following the same approach as for the total exposure (Shutdown11_m) variable. The results show that all individual exposures obtain a negative coefficient (the coefficient on food is insignificant, though). Retail and personal services obtain similar coefficients, which are negative and strongly significant (both statistically and economically). These results inform policy makers about the potential benefits of shutting down specific sectors of the economy. In particular, it points to relatively high benefits of shutting down retail activities. In fact, on top of shutdowns being fairly effective there, brick-and-mortar retail has a close substitute (online shopping) and hence, its shutdown might cause a lower loss of consumer welfare.