Spillover Effects in Empirical Corporate Finance: Choosing the Proxy for Treatment Coverage

Abstract

The existing literature indicates that spillovers can lead to a complicated bias in the estimation of causal effects in empirical corporate finance. We show that, under the assumption of simple random treatment assignment and when the proxy chosen for the group-level treatment coverage is the leave-one-out average treatment, such a spillover bias exists if and only if the average indirect effects on the treated and untreated groups are different. We quantify the gains in spillover bias reduction using Monte Carlo exercises. We propose a Wald test to statistically infer the presence of bias. We illustrate the application of this test to bear out spillovers in firms’ employment decisions.

1. Introduction

It is well known that spillovers arise in corporate finance through firm competition and geographical agglomeration; see, for example, [1], BRS21 hereon. Firm-level outcomes, such as sales or investments, depend on firms’ own treatment assignment in a given intervention and on the fraction of firms treated in the same industry and/or geographical region. As an example of these spillovers, consider the following illustration taken from BRS21. Assume that some coffee shops (i.e., the treated shops) in a given neighborhood are subject to a rise in the price of coffee beans (the treatment). The rise in the input price leads to a rise in the final price per cup of coffee for treated shops, and consequently, to a reduction in their volume of sales, i.e, the direct effect of the treatment. This is not the only effect on sales. It is likely that due to the increase in price, some consumers switch coffee shops. For coffee shops in the same neighborhood whose price has not changed, this implies an increase in the volume of sales, i.e, the spillover effect on the untreated. This spillover is an example of interference in causal inference; see, for example, [2].

Spillovers can lead to a complicated bias in the estimation of causal effects; see, for example, BRS21. Spillover bias arises when the coverage of an intervention is omitted from the analysis. In terms of the above illustration, the coverage of the intervention is the proportion of coffee shops in a neighborhood that were affected by the increase in their costs. The reduction in the volume of sales suffered by shops in the treated group could be lower if more shops in the neighborhood were affected by the increase in costs. Omitting the proportion of affected coffee shops in a given neighborhood would induce a bias in the estimation of the direct effect. The coverage of an intervention can be measured either by the group-level average or by the leave-one-out average proxy. There is a The group-level average proxy is the average number of firms in a group subject to the treatment including the firm itself. The leave-one-out average proxy is the average number of firms subject to the treatment excluding the firm itself. Little is known about which of the two proxies one should use when controlling for spillovers.

The objective of this paper is to compare the implications for the spillover bias when using the leave-one-out average or the group-level average proxy. We show that choosing the leave-one-out average proxy has two advantages. First, it simplifies the formula for the spillover bias, which facilitates its diagnosis. Second, it clarifies the definition of the average indirect effects, thereby facilitating its interpretation. These advantages justify the use of the leave-one-out average as the preferred proxy.

The leave-one-out average proxy suggests a straightforward statistical test for the diagnosis of the spillover bias. The test is a heteroskedastic-robust Wald test for the null hypothesis of equal average indirect effects on the treated and untreated groups. If this null hypothesis is rejected, the ordinary least square estimator of the average direct effect omitting the spillovers is biased. We illustrate the implementation of this test in the context of measuring the effect of credit supply contractions on firms’ employment decisions.

The rest of the paper proceeds as follows: In Section 2, we describe the two proxies to model spillovers in empirical research in corporate finance. Section 3 contains the main result and a discussion of the advantages of using the leave-one-out average as the preferred proxy. Section 4 presents results from a Monte Carlo study exploring the bias of alternative estimators of the average direct effect. Section 5 presents an illustration of the implications of our results. Section 6 concludes. Appendix A contains auxiliary calculations.

2. Framework and Graphical Representation

Let $y_{ig}$ denote an outcome, such as investments, debts, sales, or employment, for firm i belonging to group g. Group g typically represents an industry or region. Following BRS21, we assume that $y_{ig}$ is determined by

$$\begin{array}{c}\hfill y_{ig}=\phi (d_{ig},f_{ig}),\end{array}$$

(1)

where $\phi (·)$ is an unknown function, $d_{ig}$ is a treatment indicator variable, and $f_{ig}$ is the group-level treatment coverage (or intensity). The treatment indicator variable is equal to one if firm i receives the treatment, and is equal to zero otherwise. The group-level treatment coverage takes values between zero and one. The available data are a sample of size n${\{y_{ig},d_{ig},s_i\}}_{i=1}^n$, where the group variable $s_i\in \{1,\dots ,g,\dots ,G\}$ records firm i’s group. The object of study in this paper is the empirical specification of $f_{ig}$.

Causal estimands of interest include the average direct, indirect, total, and overall effects. The average direct effect is the difference between the average outcome for treated and untreated firms given all other things being equal. Following the illustration in the introduction, the average direct effect is the average change in the sales of coffee shops that experienced an increase in the price of coffee beans in the absence of spillovers. Formally, the average direct effect is

$$\begin{array}{c}\hfill {\Delta }_D:=E\left(y_{ig}\right|d_{ig}=1,f_{ig}=0)-E\left(y_{ig}\right|d_{ig}=0,f_{ig}=0).\end{array}$$

(2)

The average indirect effects are those due to treatment coverage. They can be defined by comparing the outcomes in the treated or untreated firms. Following the illustration, the average indirect effect on the treated firms is the difference in average sales for a treated coffee shop between two hypothetical situations for the group: the group is fully treated vs. the group is not treated at all. Formally, the average indirect effect on the treated is

$$\begin{array}{c}\hfill {\Delta }_T:=E\left(y_{ig}\right|d_{ig}=1,f_{ig}=1)-E\left(y_{ig}\right|d_{ig}=1,f_{ig}=0).\end{array}$$

(3)

The average indirect effect on the untreated is defined similarly:

$$\begin{array}{c}\hfill {\Delta }_U:=E\left(y_{ig}\right|d_{ig}=0,f_{ig}=1)-E\left(y_{ig}\right|d_{ig}=0,f_{ig}=0).\end{array}$$

(4)

The average total and overall effects provide summary measures combining direct and indirect effects. The average total effect is the sum of the average direct effect and the average indirect effect on the untreated:

$$\begin{array}{c}\hfill {\Delta }_{tot}:={\Delta }_D+{\Delta }_U.\end{array}$$

(5)

The average overall effect is

$$\begin{array}{c}\hfill {\Delta }_{over}:=E\left(y_{ig}\right|d_{ig}=1,f_{ig}=1)-E\left(y_{ig}\right|d_{ig}=0,f_{ig}=0)=\frac{{\Delta }_D+{\Delta }_T+{\Delta }_U}{2}.\end{array}$$

(6)

Finally, for later reference, we define the average effect at the a-coverage as

$$\begin{array}{c}\hfill {\Delta }_a:=E\left(y_{ig}\right|d_{ig}=1,f_{ig}=a)-E\left(y_{ig}\right|d_{ig}=0,f_{ig}=a),\end{array}$$

(7)

where a is a number between zero and one. Following the illustration, the average effect at the a-coverage is the difference in average sales for treated and untreated coffee shops when the group is treated at the coverage level a.

We consider two alternative models to estimate the causal estimands of interest. In the first model, the treatment assignment $d_{ig}$ is independent of the group assignment variable $s_i$. This model is a special case of the setting delineated by [2].

Spillover Model with Leave-one-out Average:

$$\begin{array}{cc}\hfill & y_{ig}={\gamma }_1+{\gamma }_2{d}_{ig}+{\gamma }_3{d}_{ig}{\tilde{d}}_{ig}+{\gamma }_4(1-d_{ig}){\tilde{d}}_{ig}+{\zeta }_{ig},\hfill \end{array}$$

(8)

$$\begin{array}{cc}\hfill & E\left({\zeta }_{ig}\right|d_{1g},\dots ,d_{ng},s_1,\dots ,s_n)=0,\hfill \end{array}$$

(9)

$$\begin{array}{cc}\hfill & d_{ig}\mathrm{and}{d}_{jg}\mathrm{are} \mathrm{independent} \mathrm{and} \mathrm{identically} \mathrm{distributed} \mathrm{for} \mathrm{all}i\ne j\in \{1,\dots ,n\},\hfill \end{array}$$

(10)

$$\begin{array}{cc}\hfill & d_{ig}\mathrm{and}{s}_j\mathrm{are} \mathrm{independent} \mathrm{for} \mathrm{all}i,j\in \{1,\dots ,n\},\hfill \end{array}$$

(11)

where

$$\begin{array}{c}\hfill {\tilde{d}}_{ig}:={(n_g-1)}^{-1}\sum _{j\ne i}{d}_{jg}1(s_j=g)1(s_i=g)\end{array}$$

(12)

is the leave-one-out average, $n_g:={\sum }_{i=1}^{n}1(s_i=g)$ is the number of firms in group g, and $1(·)$ is the indicator function, taking a value of one when the condition in parentheses is satisfied, and zero otherwise. In this model, the treatment is allocated as in the simple random treatment assignment assumption, i.e., ${\zeta }_{ig}$ is mean independent of $(d_{jg},s_j)$ for any $i,j$, $d_{ig}$ is independent of $s_j$ for any $i,j$, and $d_{jg}$ and $d_{ig}$ are independent and identically distributed for any $i\ne j$. In particular, Assumption (11) restricts the dependence between the treatment indicator variable $d_{ig}$ and the group variable $s_i$. Since $d_{ig}$ and $s_i$ are both observed, this restriction is testable and hence should not be taken as a disadvantage of the model. This model uses ${\tilde{d}}_{ig}$ as a proxy for the coverage $f_{ig}$. It delivers the approximations

$$\begin{array}{c}\hfill {\Delta }_D\approx {\gamma }_2,{\Delta }_T\approx {\gamma }_3,{\Delta }_U\approx {\gamma }_4\mathrm{and}{\Delta }_a\approx {\gamma }_2+({\gamma }_3-{\gamma }_4)a.\end{array}$$

The approximations for $\Delta$ and ${\Delta }_a$ coincide if the average indirect effects are homogeneous, i.e., ${\gamma }_3={\gamma }_4$.

In the second model, the treatment indicator $d_{ig}$ and the group variable $s_i$ can be related. Treatment in this model may not be assigned as in the simple random treatment assignment assumption. This model has been postulated by BRS21.

Spillover Model with Group-Level Average:

$$\begin{array}{cc}\hfill y_{ig}& ={\beta }_1+{\beta }_2{d}_{ig}+{\beta }_3{d}_{ig}{\overline{d}}_{ig}+{\beta }_4(1-d_{ig}){\overline{d}}_{ig}+{ϵ}_{ig},\hfill \end{array}$$

(13)

where

$$\begin{array}{cc}\hfill {\overline{d}}_{ig}& :=n_g^{-1}\sum _{j=1}^n{d}_{jg}1(s_j=g)1(s_i=g)\hfill \end{array}$$

(14)

is the group-level average treatment. This model uses ${\overline{d}}_{ig}$ as a proxy for $f_{ig}$. BRS21 shows, under additional assumptions replicated in the appendix, that this model delivers the approximations:

$${\Delta }_D\approx \underset{x\to 0}{lim}({\beta }_1+{\beta }_2+{\beta }_{3}x)-{\beta }_1={\beta }_2,{\Delta }_T\approx {\beta }_3,\mathrm{and}{\Delta }_U\approx {\beta }_4.$$

To facilitate the comparison between the two models, we now represent them using causal graphs.

Two differences arise when comparing the models. First, the proxies for coverage, and consequently, the approximations of the estimands of interest, do not coincide. While $d_{ig}$ and the group-level average ${\overline{d}}_{ig}$ are correlated, $d_{ig}$ and the leave-one-out average ${\tilde{d}}_{ig}$ are not. Notice the absence of an arrow connecting the nodes ‘Treatment’ and ‘Coverage’ in Causal Graph I. Second, while the treatment variable in the model with the leave-one-out average is assumed to follow the simple random assignment assumption, in the model with the group-level average, it is not clear whether treatment is allocated as in a more sophisticated experimental procedure. Notice the presence of the bi-directed arrow connecting the nodes ‘Treatment’ and ‘Group’ in Causal Graph II. Little is known about whether these differences are relevant and, if they are, whether one should use the group-level average or the leave-one-out average proxy. The next section spells out two advantages of using the leave-one-out proxy. These advantages illustrate, first, the relevance of the choice of proxy for the coverage and, second, the benefits obtained from the rigorous modeling of the treatment allocation procedure.

3. Main Results

To proceed, we compare the spillover bias arising from estimating ${\gamma }_2$ using a baseline model ignoring spillovers.

Baseline Model:

$$\begin{array}{c}\hfill y_{ig}={\alpha }_1+{\alpha }_2{d}_{ig}+{\xi }_{ig},E\left({\xi }_{ig}\right|d_{1g},\dots ,d_{ig},\dots ,d_{ng})=0,i=1,\dots ,n.\end{array}$$

(15)

If there are no spillovers, the OLS estimator ${\widehat{\alpha }}_2$ of ${\alpha }_2$ is an unbiased estimator of the average direct effect. BRS21 (Proposition 1) proves the following result:

Lemma 1. 

The spillover bias of the baseline estimator ${\widehat{\alpha }}_2$ for the estimand ${\beta }_2$ is:

$$\begin{array}{c}\hfill E\left({\widehat{\alpha }}_2\right)-{\beta }_2=({\beta }_3-{\beta }_4)E\left(d_{ig}\right)+{\beta }_3\frac{V\left({\overline{d}}_{ig}\right)}{E\left(d_{ig}\right)}+{\beta }_4\frac{V\left({\overline{d}}_{ig}\right)}{1-E\left(d_{ig}\right)}.\end{array}$$

(16)

We show in Appendix A that:

Proposition 1. 

The spillover bias of the baseline estimator ${\widehat{\alpha }}_2$ for the estimand ${\gamma }_2$ is:

$$\begin{array}{c}\hfill E\left({\widehat{\alpha }}_2\right)-{\gamma }_2=({\gamma }_3-{\gamma }_4)E\left(d_{ig}\right).\end{array}$$

(17)

The expression in Proposition 1 is simpler to interpret than the one in Lemma 1: ${\widehat{\alpha }}_2$ is an unbiased estimator of ${\gamma }_2$ if and only if the indirect effects on the treated and the untreated groups are homogeneous, i.e., ${\gamma }_3={\gamma }_4$. This is the first advantage of choosing the leave-one-out average proxy.

From the characterization of the spillover bias in Proposition 1, the following statistical test can statistically infer if the baseline estimator is a biased estimator of the average direct effect.

Corollary 1. 

Empirical researchers can check that the baseline estimator ${\widehat{\alpha }}_2$ is biased for the average direct effect ${\Delta }_D$ by performing a heteroskedastic-robust Wald test for the null hypothesis $H_0:{\gamma }_3-{\gamma }_4=0$ versus the alternative $H_1:{\gamma }_3-{\gamma }_4\ne 0$ based on the ordinary least squares estimator of ${\gamma }_3,{\gamma }_4$.

This check complements the heuristic guidance suggested by BRS21 by providing a test for statistically inferring the presence of spillover bias. If ${\zeta }_{ig}$ is independent of the treatment indicator variables and the group indicator variables, the homoskedastic-only Wald test is an alternative to perform this check.

What is the baseline estimator unbiased for? Since

$$\begin{array}{c}\hfill E\left(y_{ig}\right|d_{ig}=1,{\tilde{d}}_{ig}=a)={\gamma }_1+{\gamma }_2+{\gamma }_{3}a\end{array}$$

(18)

$$\begin{array}{c}\hfill E\left(y_{ig}\right|d_{ig}=0,{\tilde{d}}_{ig}=a)={\gamma }_1+{\gamma }_{4}a,\end{array}$$

(19)

one has $E\left({\widehat{\alpha }}_2\right)={\Delta }_{a=E\left(d_{ig}\right)}$ and the following corollary holds.

Corollary 2. 

The baseline estimator ${\widehat{\alpha }}_2$ is unbiased for the average effect at the average coverage ${\Delta }_{a=E\left(d_{ig}\right)}$.

The average effect at the average coverage is not equal to the sum of the average direct effect and the average indirect effect on the treated firms, which should prevent one from interpreting the baseline estimator as an unbiased estimator of the aggregation of the average direct effect and the average indirect effects (see, for example, [3]).

The second advantage of choosing the leave-one-out average proxy comes from the interpretation of the approximation ${\Delta }_T\approx {\gamma }_2$. Consider the case of a group g with two firms. Only i is treated, so ${\overline{d}}_{ig}=1/2$ and ${\tilde{d}}_{ig}=0$. In this case, there is no indirect effect on the treated firm, which is not reflected in the difference $E\left(y_{ig}\right|d_{ig}=1,{\overline{d}}_{ig}=1/2)-E\left(y_{ig}\right|d_{ig}=1,{\overline{d}}_{ig}=0)={\beta }_3/2$. Compare this result with $E\left(y_{ig}\right|d_{ig}=1,{\tilde{d}}_{ig}=0)-E\left(y_{ig}\right|d_{ig}=1,{\tilde{d}}_{ig}=0)=0$, obtained using the leave-one-out average. This suggests that ${\gamma }_3$ approximates the average indirect effect on the treated ${\Delta }_T$ that we are looking for, while ${\beta }_3$ approximates something else. Another way of interpreting this difference is that the group-level average counts ‘twice’ the effect of $d_{ig}$: by including it, first, in ${\beta }_2{d}_{ig}$, and, second, in ${\overline{d}}_{ig}$ in ${\beta }_3{d}_{ig}{\overline{d}}_{ig}$. The leave-one-out average counts only once the effect of $d_{ig}$: by including it in ${\gamma }_2{d}_{ig}$ and excluding it from ${\tilde{d}}_{ig}$ in ${\gamma }_3{d}_{ig}{\tilde{d}}_{ig}$.

4. Monte Carlo Exercises

To explore the finite sample properties of the estimator using the leave-one-out average proxy, we carry out a Monte Carlo study. We consider the specification:

$$\begin{array}{c}\hfill y_{ig}=10-4d_{ig}+{\gamma }_3{d}_{ig}{\tilde{d}}_{ig}+3.6(1-d_{ig}){\tilde{d}}_{ig}+{\zeta }_{ig},\mathrm{for}i=1,\dots ,N\in \{100,400,1600\},\end{array}$$

(20)

where ${\gamma }_3\in \{-3.6,3.6\}$ and ${\zeta }_{ig}$ has a normal distribution with mean 0 and variance 2. The design ${\gamma }_3=3.6$ has homogeneous average indirect effects and ${\gamma }_3=-3.6$ has heterogeneous average indirect effects. These values are taken from the illustration in BRS21. The treatment variable $d_{ig}$ follows a Bernoulli distribution with mean $E\left(d_{ig}\right)=0.5$. The group variable $s_i$ follows from the specification

$$\begin{array}{c}\hfill s_i=\sum _{j=1}^{6}j1(c_{j-1}<z_i^{\star }\le c_j),\end{array}$$

(21)

where $c_0=-\infty ,c_1=-1,c_2=-0.5,c_3=0,c_4=0.5,c_5=1,c_6=\infty$, and $z_i^{\star }$ is a standard normal random variable. The group variable $s_i$ is independent of the treatment variable $d_{ig}$. The disturbance term ${\zeta }_{ig}$ is independent of the covariates.

Table 1. Bias comparison of estimators.

		Heterogeneous: ${\mathit{\gamma }}_3=-3.6$		Homogeneous: ${\mathit{\gamma }}_3=3.6$
N		Baseline	Leave-One-Out	Baseline	Leave-One-Out
100	$d_{ig}$	−3.60	−0.0367	−0.0439	−0.0049
	$d_{ig}{\tilde{d}}_{ig}$		0.007		0.0433
	$(1-d_{ig}){\tilde{d}}_{ig}$		0.063		0.0569
400	$d_{ig}$	−3.60	0.0120	−0.0163	0.0195
	$d_{ig}{\tilde{d}}_{ig}$		−0.1152		−0.0502
	$(1-d_{ig}){\tilde{d}}_{ig}$		−0.0947		0.0007
1600	$d_{ig}$	−3.60	0.0053	0.0003	0.0108
	$d_{ig}{\tilde{d}}_{ig}$		0.0031		0.0182
	$(1-d_{ig}){\tilde{d}}_{ig}$		0.0155		0.0388

Note: The number of simulations is 5000.

reports the results for the bias of different estimators of ${\gamma }_2=-4$. ‘Baseline’ labels the ordinary least squares estimator from the specification (15) and ‘leave-one-out’ the ordinary least squares estimator from (8). As predicted by the theory for these experiments, the bias of the baseline estimator of the average direct effect is approximately $E\left(d_{ig}\right)({\gamma }_3-{\gamma }_4)=0.5({\gamma }_3-3.6)$, which is half of the difference between the average indirect effect on the treated and untreated firms.

5. Illustration

We now illustrate the use of the previous results in the context of applications conducted in the empirical literature. The aim is to show the advantages of using the leave-one-out average proxy to diagnose the spillover bias on the baseline estimator.

There is a growing body of empirical literature seeking to incorporate spillovers in baseline models. These papers differ in their modeling of spillovers in two dimensions. They either use the group-level average or the leave-one-out average as a proxy for the treatment coverage, and they either assume homogeneous or heterogeneous average indirect effects.

Table 2. Proxies employed in applications.

Spillover Effects ↓/Proxy →	Group-Level Average	Leave-One-Out Average
Homogeneous	[4,5]	[6,7]
Heterogeneous	[8]	BRS21

below summarizes these differences among already published papers.

Our results apply to any of these papers. We choose the application in BRS21 because the careful execution of the study lends itself to extension by applying the result in Proposition 1 (and its corollaries).

The estimand of interest is the average direct effect of a bank-lending cut (the bank in the database is Commerzbank) on German firms’ employment growth. Here, $y_{ig}$ is the symmetric growth employment rate over the 2008 to 2012 period for firm i located in county g; $d_{ig}$ is a dummy variable that equals one if the fraction of the firm’s relationship banks that are Commerzbank branches is greater or equal than 0.5, and is zero otherwise (${\mathrm{CBdep}(0/1)}_{ic}$ in BRS21’s notation); ${\tilde{d}}_{ig}$ is the average Commerzbank dependence calculated based on $d_{ig}$ of all other firms in the county g, excluding firm i itself (${\overline{\mathrm{CBdep}(0/1)}}_{ic}$ in BRS21’s notation). For the convenience of the reader, we reproduce the estimates in the table below (see BRS21, Table 5, Columns (4) and (6)).

By comparing the baseline estimate ${\widehat{\alpha }}_2=-0.028$ with ${\widehat{\gamma }}_2=-0.053$ in

Table 3. Estimates from BRS21.

	(1)	(2)
$d_{ig}$	−0.028	−0.053
	(0.006)	(0.017)
$d_{ig}{\tilde{d}}_{ig}$		0.025
		(0.068)
$(1-d_{ig}){\tilde{d}}_{ig}$		−0.115
		(0.038)

Note: The dependent variable is the symmetric growth rate of firm employment from 2008 to 2012. Robust standard errors, clustered at the county level, are in parentheses. Source: BRS21 (Table 5).

, BRS21 infers that ignoring spillovers causes the baseline estimator to be biased for the average direct effect. This comparison, however, does not take into account sampling variability, which, as we are going to show below, can change the above inference.

The estimate ${\widehat{\gamma }}_3$ is 0.025, whereas the estimate ${\widehat{\gamma }}_4$ is −0.115. To verify that this difference is not only due to sampling variability, Corollary 1 proposes a Wald test. Performing this test is straightforward. It requires the Wald test statistic to be computed:

$$W=\frac{{(\widehat{{\gamma }_3}-\widehat{{\gamma }_4})}^2}{s{e}_{\widehat{{\gamma }_3}}^2+s{e}_{\widehat{{\gamma }_4}}^2-2\widehat{cov}(\widehat{{\gamma }_3},\widehat{{\gamma }_4})},$$

where $\widehat{{\gamma }_3}$ and $\widehat{{\gamma }_4}$ are the OLS estimators for the estimands ${\gamma }_3$ and ${\gamma }_4$, $s{e}_{\widehat{{\gamma }_3}}$ and $s{e}_{\widehat{{\gamma }_4}}$ are their respective standard errors, and $\widehat{cov}(\widehat{{\gamma }_3},\widehat{{\gamma }_4})$ is the covariance estimator. The asymptotic null distribution of the Wald statistic is a chi-squared distribution with one degree of freedom, from which we can compute critical values. The Wald test suggests rejecting the null hypothesis (and statistically inferring that the baseline estimator is biased for the average direct effect) if the realized value of the Wald test statistic is greater than or equal to the critical value.

Table 3 contains all of the values to compute the realized value of the Wald test statistic, except for $\widehat{cov}(\widehat{{\gamma }_3},\widehat{{\gamma }_4})$. For illustrative purposes, we take two values: a lower bound of zero and an upper bound from the Cauchy–Schwarz Inequality. In the case of the upper bound, the realized value of the Wald statistic is

$$w=\frac{{[0.025-(-0.115)]}^2}{0.{068}^2+0.{038}^2-2\times 0.00258}=\frac{0.0196}{0.0009}=21.77,$$

while the critical value at the $99\%$ confidence level is $c{v}_{0.99}=6.63$. Since the realized value of the statistic ($w=21.77$) is greater than the $99\%$ critical value ($c{v}_{0.99}=6.63$), the test indicates that the baseline estimator is biased for the average direct effect. However, the baseline estimator is still an unbiased estimator for the average effect at the average coverage (Corollary 2). In the case of the lower bound, the realized value of the statistic ($w=3.23$) is smaller than the $99\%$ critical value ($c{v}_{0.99}=6.63$). In such a case, Proposition 1 indicates that there is no evidence that the baseline estimator is a biased estimator of the average direct effect. We conclude, from the estimates in Table 3, that one cannot infer that ignoring spillovers causes the baseline estimator to be biased for the average direct effect. We remark that these results are not immediately available if one chooses the group-level average as a proxy for the coverage.

6. Conclusions

Competitive interactions and agglomeration among firms generate spillovers after a shock, a change in regulation, or any kind of intervention affecting firms. Ignoring these spillovers when estimating causal effects leads to biased estimation. This paper discusses the choice between two alternative proxies for modeling spillovers. We show that this choice is relevant for diagnosing the existence of spillover bias. The leave-one-out average proxy has two advantages over the group-level average proxy. First, it simplifies the formula for the spillover bias, thereby facilitating its diagnosis. The baseline estimator is unbiased for the average direct effect if and only if the average indirect effects are homogeneous. Second, it clarifies the definition of the average indirect effect on the treated firms, thereby facilitating its interpretation. These advantages justify the use of the leave-one-out average as the preferred proxy and suggest a straightforward test to statistically infer the existence of spillover bias.

One natural extension is to investigate how to define the coverage proxy when the treatment is continuous instead of binary. This extension is outside of the scope of this paper and is left for future research.