## Abstract

Conventional wisdom suggests that labor unions raise worker wages, while the newer empirical literature finds only negligible earnings effects. I reconcile this apparent contradiction by arguing that collective bargaining targets fringe benefits. Using U.S. firm-level data from the Bureau of Economic Analysis (BEA) Multinational Enterprise Survey and Compustat, I exploit a regression discontinuity in majority rule union elections to compare changes in employee compensation at firms whose establishment barely won a union election against those that barely lost an election. Following unionization, average employee compensation and employer pension contributions increase, which raises the labor share of compensation.

## I. Introduction

IT is widely believed that labor unions increase employer costs by using their bargaining power to negotiate higher wages, yet there exists surprisingly little recent evidence to support this suggested causal relationship (Lewis, 1986; Freeman & Kleiner, 1990; Lalonde, Marschke, & Troske, 1996; DiNardo & Lee, 2004; Frandsen, 2014). That such an extensive literature exists is a testament to the historical role of labor unions in shaping the employer-employee relationship, along with the growing interest in the impact of the erosion of union influence on U.S. labor relations since the early 1980s. As recently as April 2016, however, unions representing nearly 40,000 employees of Verizon, the largest telecommunications company in the United States, organized a strike precisely because the company proposed cutting health care and retirement benefits despite reportedly offering wage concessions of 6%.1

In this paper, I consider and test whether collective bargaining agreements primarily target employee benefits rather than wages. While theory remains largely agnostic on the extent to which unionism affects compensation through wages or benefits, empirical studies have tended to rely on the former as a proxy for labor compensation due to a relative lack of reliable measures of the latter. I contribute to this strand of literature by identifying credibly these effects in a setting where good measures of benefits are indeed available.

And though excluded from standard measures used to estimate the earnings effects of various economic policies, nonwage compensation accounted for nearly one-quarter of total compensation in 1997 according to the Bureau of Labor Statistics' Employer Cost Index (ECI). Worker benefits growth has since continued to outpace wage growth from 2005 through 2015, increasing the average benefits-to-wage ratio from .42 to .46 over the same period.

Moreover, there exists a positive relationship between unionism and fringes (Solnick, 1978; Freeman, 1981; Leigh, 1981; Alpert, 1982; Feldman & Scheffler, 1982; Feuille, Delaney, & Hendricks, 1985; Allen & Clark, 1986; Freeman, 1986; Zax, 1988; Budd, 2004). Union employees are more likely to be covered by a pension plan (Fosu, 1983, 1984; Freeman & Medoff, 1984; Freeman, 1985; Bloom & Freeman, 1992; Montgomery & Shaw, 1997; Wunnava & Ewing, 1999) and employer-sponsored health insurance (Rossiter & Taylor, 1982; Fosu, 1984; Buchmueller, DiNardo, & Valletta, 2002). They earn more vacation time (Green & Potepan, 1988; Farber et al., 2018) and mandated benefits (Weil, 1996), such as workers' compensation (Hirsch, Macpherson, & DuMond, 1997) and unemployment benefits (Budd & McCall, 1997, 2004). Sojourner and Pacas (2019) even show that by increasing access to health insurance, union membership exerts a positive net fiscal impact.

Fringes aside, cross-sectional estimates of the union wage premium are between 15% and 25%, while longitudinal estimates are closer to 10% (Feldman & Scheffler, 1982; Freeman, 1984; Lewis, 1986; Kornfeld, 1993; Wunnava & Peled, 1999; Budd & Na, 2000; Blanchflower & Bryson, 2004). The latter estimates are typically based on workers joining or leaving a unionized workplace relative to a control group (Freeman & Kleiner, 1990).

Related work captures how the wage impact of unionism varies across the distribution of earnings. Freeman (1980b, 1984) shows that unions decrease wage dispersion. This literature, having since adopted quantile methods, has continued to find that unionization compresses the wage distribution (Chamberlain, 1994; Card, 1996; Firpo, Fortin, & Lemieux, 2009; Fortin et al., 2011; Frandsen, 2012). Conversely, Juhn, Murphy, and Pierce (1993), DiNardo, Fortin, and Lemieux (1996), DiNardo and Lemieux (1997) and Farber et al. (2018) show that the deunionization movement contributed notably to the rise in U.S. wage inequality in the 1980s. Labor shares of income have also fallen most sharply in industries experiencing the largest declines in union membership rates (Abdih & Danninger, 2017). Yet these prior estimates capture the wage effect of joining firms with unions already in place rather than the effect of new unionization. This paper focuses on the latter question.

Establishment-level difference-in-differences estimates from union organizing drives show scant wage gains, though they display an uptick in working conditions and some benefits (Freeman, 1986; Freeman & Kleiner, 1990; Lalonde et al., 1996). Positive wage effects remain elusive too when using quasi-experimental regression discontinuity methods to compare close union election winners and losers (DiNardo & Lee, 2004; Frandsen, 2014).

Frandsen (2014) notes that establishment-level studies of the union wage premium cannot discern the price effect—the union premium for a given worker's skill level—from the composition effect—how unionization alters the distribution of worker skill level. He instead uses matched employer-employee data to study worker-level compensation for stayers, leavers, and new arrivers at the establishment. He estimates a negative composition effect (i.e., older, higher-paid workers leave and are replaced by younger, cheaper ones) and a null price effect as workers who stay with the unionized firm experience no change in wages.

Yet if the distribution of worker benefits is more uniform than that of wages, negative composition effects should reduce wages proportionally more than they do compensation. Indeed, the federal tax code requires that employers offer fringe benefits in a nondiscriminatory manner for “similarly situated” workers so as to maintain favorable tax treatment for self-insured health plans and employer pensions (Collins, 1999; Simon & Kaestner, 2004).2 These rules in turn provide a binding constraint on within-firm benefits inequality that simultaneously increases wage inequality (Carrington, McCue, & Pierce, 2002).

I combine National Labor Relations Board (NLRB) union election results from 1983 to 2009 with firm-level data from the Bureau of Economic Analysis's Multinational Enterprise (MNE) survey to examine the effect of union certification on firm-level average wages and on average worker compensation. Because MNE wage data are reported distinctly from other nonwage compensation only in benchmark survey years (1989, 1994, 1999, 2004), I provide a descriptive analysis of how a firm's workers' wages evolve over time according to whether a union won or lost its election in an intervening year. Here I replicate the results found in the earlier works of Freeman and Kleiner (1990), Lalonde et al. (1996), DiNardo and Lee (2004), and Frandsen (2014), showing that workers at unionizing firms experience no change in wages relative to those who do not unionize, though with limited precision. Next, I estimate the relationship between union certification and total worker compensation in a hybrid differences-in-differences and regression-discontinuity framework by comparing changes in average worker compensation at firms with an establishment that barely wins a secret ballot union election against those that barely lose the election. This departs slightly from the traditional regression-discontinuity approach as not all of the requisite assumptions are satisfied. Nonetheless, I find that union certification increases average worker compensation by 7% to 10%, which accounts for $4,800 to$6,900 annually (in 2016 dollars).

However, because I can only track firm-level average employee compensation, I am unable to distinguish effects among stayers from effects arising due to compositional changes among the firm's workforce. Nonetheless, given the results from Frandsen (2014)—that unionization induces negative selection while the wages of stayers are unaffected—the current study's estimates reflect a combination of the total compensation composition effect and the change in benefits among stayers. If unionization induces negative selection along the skill distribution, my estimates should be considered a lower bound on the total compensation effect for stayers (i.e., the price effect). If instead unionization shifts the skill distribution to the right, the total compensation effect among stayers would be bounded above by the study's estimates. In either case, I am constrained to capturing merely the extent to which certification raises the average combined wages and benefits of a firm's employees, both new and old.

I also replicate the same study design on a small sample of firms from the Compustat database, where identical compensation results emerge. In addition, union certification increases employer contributions to its employees' pension plans by more than 20%, or $400 to$750 per worker per year. In light of the null union wage effects recovered in both the current firm-level study and prior establishment-level studies, these combined findings suggest that collective bargaining efforts target employee benefits more than they do wages.

Against the backdrop of these empirically inharmonious union effects, the current study's results are particularly resonant with those of Lee and Mas (2012), who find that a union victory at an establishment reduces its enveloping firm's stock price by 10% in an event-study framework.3 Such a loss corresponds to a $20 million decline in market value, in 1998 dollars. That establishment-level union elections, which Lee & Mas (2012) retained so long as the fraction of total firm employees represented on the ballot exceeded just 5%, had such a disproportionately large impact on the overall profitability of the firm underscores the outsized role of spillover effects across other establishments within a firm. The elections considered in the current study account for similarly low levels of worker representation. It is hard to fathom how either effect could materialize in the absence of formidable intrafirm “union threat effects,” whereby the firm—motivated solely by the desire to preempt the spread of further unionization or possessing a more general preference for minimizing differences in average worker compensation across its plants—offers similarly sized concessions to workers at directly unaffected establishments. Indeed, this channel proves essential as each successive unionization within a firm increases average compensation by less than had the previous one. The enormity of these implied spillover effects may explain why managerial resistance to unionization is so staunch despite the small wage effects uncovered in prior studies; the pro-union votes of fewer than 1% of the workers at a firm produce compensation gains of 7% to 10%, on average, for all of the firm's employees. Reassuringly, however, I find that the large, positive effects found here are concentrated among smaller firms for which the number of workers participating in the election represents a sizable fraction of the firm's workforce. Whatever the mechanism, Lee and Mas (2012) rationalize the dip in equity as the combination of a transfer of wealth from owners to workers plus efficiency losses, but data limitations preclude the authors from characterizing the contribution of either channel. My findings provide an answer to this heretofore unanswered question: the 10% decline in equity amounts to a loss of$59,600 per unionized worker—or $8,340 per worker across all workers.4—and the compensation gains implied by the current study's estimates are between$5,500 and $7,800 per worker (all in 2016 dollars). Alternatively, 65% to 93% of the equity loss from union certifications accrues to workers in the form of compensation gains, while the remaining 7% to 35% (or$540 to $2,840 per worker) consitute efficiency losses due to unions, suggesting that much of the union-generated equity loss is captured by workers.5 The next section describes NLRB union elections, while section III describes the firm-level data. Section IV details the identification challenges and techniques used to overcome them. Section V presents results on how total compensation and employer pension contributions respond to a union certification. Section VI summarizes and concludes. ## II. Background on the Union Election Process The National Labor Relations Act (NLRA) outlines the process by which a group of workers may obtain legal recognition as a union.6 Though the typical route to unionization involves a National Labor Relations Board (NLRB) secret ballot election, employers do have the option of voluntarily recognizing and bargaining with a union in the absence of an election (DiNardo & Lee, 2004; Brudney, 2005; Frandsen, 2014).7 The more common procedure has three main steps: a union organizing drive, an election, and certification.8 In a union organizing drive, the union must collect the signatures of at least 30% of a proposed bargaining unit on a petition expressing support for union representation. The union organizer then submits the petition to the NLRB, which decides whether to accept the petition (which requires that the proposed group of workers share a collective interest that can be adequately represented in bargaining) and which categories of employees qualify for the union's bargaining unit (DiNardo & Lee, 2004). If accepted, the NLRB holds a secret ballot election at the place of work. A union wins the election if it receives a strict majority of votes. The NLRB then certifies victorious unions as the sole representative of the bargaining unit. Employers must subsequently bargain with the union “in good faith.” Following the election, such bargaining is intended to culminate in agreement to a first contract between the union and employer. However, this process does not always reach such a conclusion. Since all successful elections in the data are coded as a union win, whether or not a first contract is struck, the interpretation of the results is modified accordingly. In particular, the change in compensation resulting from union victories reflects the average effect of union election wins that obtain and do not obtain a collective bargaining agreement or, more concisely, the effect of NLRB certification. Nonetheless, it would be difficult to justify the presence of union compensation effects if union election victories did not, in fact, increase the likelihood that an agreement is reached. To test this, DiNardo and Lee (2004) first note that parties to collective bargaining agreements are required to file notices with the Federal Mediation and Conciliation Services (FMCS) at least thirty days prior to the termination or modification of an existing contract. While compliance with this law is imperfect, these authors examine how the probability of filing such a thirty-day notice, interpreted as a proxy for signing a first contract, evolves according to the union vote share. Indeed, this probability jumps by over 20 percentage points just above the 50% vote share threshold, indicating that union victories do increase the likelihood of reaching a collective bargaining agreement. Contracting issues notwithstanding, the secret ballot election should theoretically generate ex ante uncertainty over the election outcome; neither the union nor the employer will know whether the union is one vote away from victory or defeat until all of the votes have been cast and counted. This feature is econometrically useful, as close union winners and close union losers are effectively randomly assigned. One could then use a regression-discontinuity framework to estimate the effect of unionization on labor market outcomes.9 In reality, however, disputes and delays can compromise the integrity of the election process in a number of ways.10 For example, the employer or union may allege claims of unfair labor practices at any stage of the election process. These are any actions by the employer or employee that violate the so-called laboratory conditions required for valid secret ballot elections. If the charges are upheld by the NLRB, the election results can be cast aside (Moberly, 2002). Moreover, these charges may be filed after close election losses, which could generate nonrandom sorting around the majority rule threshold. Additionally, either party may challenge the validity of individual ballots before or during the election. The NLRB then rules on whether to count the challenged ballots whenever the votes prove pivotal. On the basis of these rulings, the election outcome may be erased or even overturned. These sources of ex post selection can potentially invalidate the regression-discontinuity design, which requires that manipulation of the running variable (in this case, the vote count) is impossible. In the sections that follow, I devote considerable discussion to the extent to which these concerns are justified in the data and on how to correct for this source of confounding bias so as to recover a causal interpretation of the effects of union victories. ## III. Data and Sample Construction ### A. Union Elections This study begins with an exhaustive set of NLRB union representation and decertification elections from 1983 through 2009, collected and maintained by Henry Farber.11 Each observation corresponds to a union election held at an establishment. The record includes the name and address of the employer, the number of votes collected for and against the union, the date of the election, and the election result. Table 1 presents summary statistics on these 990 firm-matched union elections12 across which 170,000 votes were cast.13 Unions were victorious 36% of the time, while the average number of voters and pro-union vote share were 171 and 46%, respectively. Table 1. NLRB Elections Summary Statistics MNE SampleCompustat Sample (Compensation) AllUnion LossUnion WinAllUnion LossUnion Win Union win (%) 34.5 100 41.1 100 Vote share 45.7 34.5 67.1 44.6 37.3 61.6 Number of votes (average) 174.9 195.4 135.9 148.5 157.3 135.9 Number of votes (total) 144,629 105,900 38,729 24,208 15,101 9,107 Number of elections 827 542 285 163 96 67 Benchmark MNE Sample Compustat Sample (Pensions) All Union Loss Union Win All Union Loss Union Win Union win (%) 38.4 100 35.6 100 Vote share 45.0 37.1 57.8 45.9 39.1 58.1 Number of votes (average) 173.5 210.2 114.6 134.4 159.1 89.7 Number of votes (total) 71,835 53,611 18,224 35,080 26,736 8,344 Number of elections 414 255 159 261 168 93 MNE SampleCompustat Sample (Compensation) AllUnion LossUnion WinAllUnion LossUnion Win Union win (%) 34.5 100 41.1 100 Vote share 45.7 34.5 67.1 44.6 37.3 61.6 Number of votes (average) 174.9 195.4 135.9 148.5 157.3 135.9 Number of votes (total) 144,629 105,900 38,729 24,208 15,101 9,107 Number of elections 827 542 285 163 96 67 Benchmark MNE Sample Compustat Sample (Pensions) All Union Loss Union Win All Union Loss Union Win Union win (%) 38.4 100 35.6 100 Vote share 45.0 37.1 57.8 45.9 39.1 58.1 Number of votes (average) 173.5 210.2 114.6 134.4 159.1 89.7 Number of votes (total) 71,835 53,611 18,224 35,080 26,736 8,344 Number of elections 414 255 159 261 168 93 Data are from matched NLRB union elections with corresponding firms in the BEA Multinational Survey and Compustat database, respectively. For the Benchmark MNE Sample, data are from matched NLRB union elections with corresponding firms in the 1989, 1994, 1999, and 2004 editions of the BEA Multinational Survey. ### B. Worker Compensation Firm-level data on employment and worker compensation, extracted from two unique sources, give rise to three samples. The primary sample is derived from the BEA Multinational Enterprise Survey, which tracks balance sheet and income statement variables for a panel of approximately 2,500 U.S.-based firms that own subsidiary companies operating outside the home country from 1983 to 2009.14 Importantly, employee compensation is reported at the firm level, which implies that union compensation effects will be detectable only when either the bargaining unit is relatively large or when establishment-level union spillovers are large enough to affect average employee compensation at the enveloping firm. These firms tend to be strikingly larger than the typical U.S. firm, averaging just shy of 28,000 employees as compared to the roughly 250 employees per firm in the Longitudinal Business Database (LBD; Frandsen, 2014). Table 1 indicates that 827 such union election-holding firms are included in the sample. With an average vote count of 174.9, union election ballots represent approximately 145,000 voting workers. To the extent that establishment-level union election results affect other establishments within the firm, the group of potentially affected employees is just above 23 million workers (827 firms $×$ 28,000 employees per firm) of the annually averaged 119 million employees working between 1983 and 2009.15 The secondary sample is derived from the Compustat database, comprising a panel of more than 9,000 publicly traded U.S. companies dating back to 1950 for which balance sheet, cash flow, pension, and income statement data are available from 1983 to 2009. In addition to providing employee compensation data that can serve as a validity check on the main results, these data provide a glimpse into one important nonwage benefit provided by firms: employer contributions to its workers' pension plans.16 Table 2 shows that these companies are also predominantly large firms, averaging just over 33,000 employees across the 163 firms whose affiliated establishment held a union election. These elections tend to be slightly smaller, accounting for 148.5 voting members per ballot, or just over 24,000 worker votes overall. The number of potentially affected employees approaches 5.4 million (163 firms $×$ 33,000 employees/firm).17 Table 2. Average Firm Characteristics MNE SampleCompustat Sample (Compensation) AllUnion LossUnion WinAllUnion LossUnion Win Employment Preelection 27,635 27,724 27,469 33,120 34,830 29,949 Postelection 27,832 28,223 27,102 33,419 35,572 29,428 Compensation Preelection$68,845 $71,053$64,747 $77,686$77,061 $78,994 Postelection$70,361 $71,787$67,697 $77,751$75,016 $83,651 Benchmark MNE Sample Compustat Sample (Pensions) All Union Loss Union Win All Union Loss Union Win Employment Preelection 21,036 20,639 21,703 30,586 30,911 30,010 Postelection 20,645 20,727 20,504 32,411 33,052 31,273 Wages Pension Contributions Preelection$55,974 $55,979$55,966 $1,651$1,800 $1,410 Postelection$57,847 $57,621$58,227 $2,069$1,973 $2,224 MNE SampleCompustat Sample (Compensation) AllUnion LossUnion WinAllUnion LossUnion Win Employment Preelection 27,635 27,724 27,469 33,120 34,830 29,949 Postelection 27,832 28,223 27,102 33,419 35,572 29,428 Compensation Preelection$68,845 $71,053$64,747 $77,686$77,061 $78,994 Postelection$70,361 $71,787$67,697 $77,751$75,016 $83,651 Benchmark MNE Sample Compustat Sample (Pensions) All Union Loss Union Win All Union Loss Union Win Employment Preelection 21,036 20,639 21,703 30,586 30,911 30,010 Postelection 20,645 20,727 20,504 32,411 33,052 31,273 Wages Pension Contributions Preelection$55,974 $55,979$55,966 $1,651$1,800 $1,410 Postelection$57,847 $57,621$58,227 $2,069$1,973 $2,224 Compensation per worker, employer pension contributions per worker, and wages per worker are reported in 2016 dollars. For the MNE Benchmark Sample, pre- and post-means are separated by the five intervening years between surveys. Though a sizable fraction of the U.S. workforce is employed by the firms with an establishment undergoing unionization during the study's sample, it would be a mistake to consider these firms representative of the typical U.S. company.18 Rather, the firms in this study were chosen because they deliver worker compensation and benefits measures in lieu of the standard wage and salary earnings measures. Table 2 further partitions summary statistics according to whether firms won or lost a union election. Consistent with Frandsen (2014), union winners experience a small decrease in employment relative to union losers.19 In contrast to Frandsen (2014), however, union winners show a relative increase in average worker compensation as compared to union losers. Average total worker earnings in the current study also exceed those in Frandsen (2014) by approximately$21,000 per year (after converting average earnings reported in Frandsen, 2014, to year 2016 dollars). This difference, in turn, constitutes 30% of the total compensation measure, which matches the national average benefits to wage ratio over the relevant time period.20 Finally, union winners are the beneficiaries of a relatively larger increase in employer contributions to worker pension plans than are union losers.

Finally, a third sample, which is more precisely a subsample of the BEA MNE Survey, consists of worker wage data from four of the benchmark survey years: 1989, 1994, 1999, and 2004. Every five years, the BEA circulates a more comprehensive questionnaire to multinational enterprises that elicits wages apart from total employee compensation. Though the infrequent periodicity of the panel somewhat inhibits its utility for making causal inferences, this shortcoming is overshadowed by its provision of a path for directly reconciling the current study's results with those of earlier studies examining the wage consequences of unionization. Specifically, I use these data to unveil how firm wages might evolve differently on the basis of whether one of its constituent establishments won or lost its union election held in one of the between-survey years. In terms of the distribution of election outcomes, table 1 shows that the MNE Benchmark Survey sample is not dissimilar from the larger survey from which it originates. These 414 elections yield an average win rate of 38.4 and vote count of 173.5, and cover half the number of voters as does the annual survey.

That said, table 2 demonstrates that the benchmark survey firms have fewer employees—averaging just under 21,000 per firm—than do their full survey counterparts. Average wage growth rates among union winners and losers are not statistically different, and even less so after converting them to an annual rate. I explore the extent to which this seemingly convergent wage growth trend holds up to further statistical scrutiny in appendix section A.

### C. Procedure for Matching Union Elections to Firms

To match the union election results with the characteristics of the firm whose establishment held each union election in both the MNE and Compustat databases, I first standardized the employer's name. Using an automated record-linkage program developed by Blasnik (2010) and Wasi and Flaaen (2015), I then merged 827 establishment union elections in the NLRB database with their enveloping BEA MNE firms on the basis of the strength of the recorded match supplemented with a manual verification of the company name concordance.21 Note that the resulting matched analytic subsamples include only firms for which a three-year contiguous panel of populated employee compensation data exists.22

## IV. Regression Framework and Identification

### A. Identification of Union Effects

The central challenge of answering how union certifications affect worker compensation is that whether a firm is unionized is not random. Firms that are unionized may be different along important observable and unobservable dimensions, including the structure of employee compensation packages. Simple comparisons between union and nonunion firms will not capture the causal link between union representation and worker compensation.

However, union representation is decided on the basis of whether the employee vote reaches a strict majority in favor of the proposed collective bargaining authority. If firms that barely lose a union election (e.g., receive 49% of the vote) and firms that barely win a union election (e.g., receive 51% of the vote) are otherwise similar, differences in the corresponding outcomes will reflect the causal effect of union certification. This is precisely the logic that motivates past attempts to identify union effects by way of the regression discontinuity design (DiNardo & Lee, 2004; Lee & Mas, 2012; Sojourner et al., 2015).23

Following Frandsen (2014), let $D=1(R>r0)$, where $D$ is an indicator for union victory, $R$ is the union vote share, and $r0$ is the majority rule threshold. Furthermore, let observed outcome $Y=Y0+(Y1-Y0)D$, where $Y1$ is the potential outcome associated with a union victory and $Y0$ is the potential outcome associated with a union defeat. If the conditional distribution of these potential outcomes with respect to the union vote share is continuous near the majority rule threshold of $R=r0$, then the difference in the conditional distribution of $Y1$ and $Y0$ at the threshold represents the causal effect of union certification on the outcome. As in Frandsen (2014), the previous identifying assumption is as follows:

Local Continuity: $FYd|R(y|r)$ is continuous in $r$ at $r=r0$, for $d∈{0,1}$.

In practice, this assumption will hold provided that there is ex ante uncertainty over the outcome of close union elections (Lee, 2008). Uncertainty over the outcome increases with the number of voters, and so past researchers using this design often restrict the study sample to elections garnering at least twenty votes (DiNardo & Lee, 2004; Lee & Mas, 2012; Frandsen, 2014; Sojourner et al., 2015). Nonetheless, the local continuity assumption will be violated if either employers or unions can alter the results of the election after initial ballots are cast. The ability to challenge individual ballots and allege unfair labor practices, in particular, may engender ex post manipulation of the running variable.

Local continuity cannot be directly tested but does imply that the density of $R$ and conditional distribution of pretreatment characteristics are continuous at the majority rule threshold, $R=r0$ (Frandsen, 2014). Tests of these corollary implications have become a standard part of analyses that use a regression discontinuity design (Imbens & Lemieux, 2008; McCrary, 2008; Lee & Lemieux, 2010).

If these tests do reveal discontinuities in the density of the running variable or conditional distribution of pretreatment characteristics, then local continuity is not a valid assumption. In its place, Frandsen (2014) proposes replacing local continuity with a weaker assumption that exploits the panel nature of the data. One such identifying assumption is a hybrid of the regression discontinuity and differences-in-differences approach. Again, following Frandsen (2014), let $Y-1$ be the preelection outcome and define $Δd≡Yd-Y-1$ as the potential change in outcome following the union election. Then one can make the alternative identifying assumption on the conditional distribution of $Δd$:

Local continuity in differences: $FΔd|R(y|r)$ is continuous in $r$ at $r=r0$, for $d∈{0,1}$, where $FΔd|R(y|r)$ is the conditional cdf of changes in the outcome variable as a function of the vote share.

Local continuity in differences will hold if the factors driving selection around the majority rule threshold have a time-invariant effect on the outcome. This is the analog of the parallel trends assumption.

Under the traditional RD assumption (local continuity), the causal effect of unionization on postelection outcomes is given by the difference in conditional postelection means just above and below the threshold for determining treatment. Under local continuity in differences, the causal effect is given by the difference in conditional means before and after the election at either side of the threshold.

### B. Estimation Framework

My estimation approach also follows that of Frandsen (2014), which is based on the techniques introduced by Porter (2003) and Lee and Lemieux (2010). The standard local linear specification uses weighted least squares (WLS) to estimate the following:1
$Yi=β0+δDi+β1Ri+β2RiDi+εi.$
(1)
Weights $wi=KRih$, where $K$ is a kernel function and $h$ is the chosen bandwidth. The estimate of $δ$ is interpreted as the local average treatment effect on $Y$ at the cutoff point. This framework can also be used as a specification check on the local continuity assumption by replacing postelection outcomes with preelection outcomes. To test whether $R$ exhibits any discontinuities, I employ the methodology developed by McCrary (2008).
If local continuity is shown to be a specious assumption, one can instead invoke local continuity in differences to estimate the effect of unionization on outcomes. In this latter case, the estimating equation is
$Yi-Yi,-1=β0+δDi+β1Ri+β2RiDi+εi,$
(2)
where $Yi,-1$ is the preelection outcome and weights are equivalent to those in equation (1). This is a local linear difference-in-differences approach that estimates $δ$ by taking the difference in pre- and postelection outcomes at either side of the threshold.

Finally, I normalize the running variable, $Ri$, in two different ways as in Frandsen (2014). First, I set the running variable equal to the vote share and remove all elections receiving fewer than $k$ votes. The raw vote share is then mapped to its corresponding $100/k$-percent bin. These procedures avoid mechanical discontinuities in the vote share due to differences in election sizes. (See DiNardo & Lee, 2004, for further explanation.) The second method expresses $Rialt$ as the union margin of victory.

In the first series of specifications, I follow Frandsen (2014) in choosing ad hoc bandwidths corresponding to elections whose victory margin is less than 20% and 15%, respectively.24 In addition, I reestimate equation (2) after implementing the Imbens and Kalyanaraman (2012) procedure for optimal bandwidth selection, as well as after using a 10% victory margin bandwidth in order to assess the robustness of the results. Heeding the insights of Gelman and Imbens (2018), I restrict the local polynomial specification to those that are linear and quadratic in the vote share across all bandwidth choices.

As Frandsen (2014) notes, the share-based running variable gives greater weight to larger elections, while the tally-based running variable favors smaller elections. However, excluding all elections with fewer than twenty votes diminishes the relative importance of which running variable specification is chosen. I present the results using both the share-based running variable and the tally-based running variable in the analysis.

## V. Results

### A. Evidence of Nonrandom Selection

From the vote share density graphs, there arises unequivocal evidence of sorting around the majority rule threshold. Figures 1a and 1b show the distribution of the union vote share (tabulated by 5 percentage point bins) for the MNE and Compustat samples, respectively. Too few close union victories appear relative to what one would expect in the absence of any manipulation of the vote share variable. In particular, the McCrary (2008) test strongly rejects continuity of the running variable with an authoritative degree of confidence ($t$-statistic $≈$18 in the MNE sample and t-stat $≈$10 in the Compustat sample).25 The Frandsen (2017) test also rejects the null hypothesis of no vote manipulation ($p$-value ranges between 0.001 and 0.004 in the MNE sample and is between 0.009 and 0.010 in the Compustat sample). These discontinuities are robust to the way in which the running variable is constructed. For example, appendix figures 2 and 3 exhibit similarly large declines in density at and just above the 0 margin-of-victory threshold in the vote count.

Figure 1.

Union Vote Share Distributions

Panel a illustrates the density of union vote shares for all 827 NLRB elections with at least twenty voters matched to firms in the BEA Multinational Enterprise Survey. Panel b illustrates the density of union vote shares for all 163 NLRB elections with at least twenty voters matched to firms in the Compustat sample.

Figure 1.

Union Vote Share Distributions

Panel a illustrates the density of union vote shares for all 827 NLRB elections with at least twenty voters matched to firms in the BEA Multinational Enterprise Survey. Panel b illustrates the density of union vote shares for all 163 NLRB elections with at least twenty voters matched to firms in the Compustat sample.

Figure 2.

Compensation by Union Vote Outcomes across Time, Close Elections

Panel a shows how log average employee compensation evolves for 278 firms whose unions lost the vote by 20% or less (in red) as compared to 145 firms whose unions won the vote by 20% or less (in blue). Panel b shows how log average employee compensation evolves for 215 firms whose unions lost the vote by 15% or less (in red) as compared to 115 firms whose unions won the vote by 15% or less (in blue).

Figure 2.

Compensation by Union Vote Outcomes across Time, Close Elections

Panel a shows how log average employee compensation evolves for 278 firms whose unions lost the vote by 20% or less (in red) as compared to 145 firms whose unions won the vote by 20% or less (in blue). Panel b shows how log average employee compensation evolves for 215 firms whose unions lost the vote by 15% or less (in red) as compared to 115 firms whose unions won the vote by 15% or less (in blue).

Figure 3.

Change in Average Log Compensation, by Vote Share

Panel a shows the change in log compensation by union vote share for 827 matched BEA MNE Survey firms and NLRB union election results, and panel b does so for the 163 matched Compustat firms and NLRB union election results. The left sides of the panels show the change from two years prior to the election to one year prior to the election, while the right panels show the change from one year prior to the election to one year after the election. The plot displays conditional means and 95% confidence intervals by vote share bins with width .05 (and 0.10).

Figure 3.

Change in Average Log Compensation, by Vote Share

Panel a shows the change in log compensation by union vote share for 827 matched BEA MNE Survey firms and NLRB union election results, and panel b does so for the 163 matched Compustat firms and NLRB union election results. The left sides of the panels show the change from two years prior to the election to one year prior to the election, while the right panels show the change from one year prior to the election to one year after the election. The plot displays conditional means and 95% confidence intervals by vote share bins with width .05 (and 0.10).

These patterns indicate that not only is there nonrandom sorting around the determinative threshold for assigning union victories, but that the postelection manipulation is disproportionately more likely to result from the obstructive actions of the employer rather than the union. This type of ex post manipulation of election results is consistent with the findings of Frandsen (2014). Additional evidence documenting the nature of sorting about the threshold is provided in appendix B.

One potential work-around that may be used to circumvent this election manipulation issue is to restrict the sample to the first such election observed at a firm, as in Sojourner et al. (2015). Repeat elections may provide unions or management with additional opportunities to learn and apply tactics for manipulating the election outcome, such as challenging individual ballots. Excluding noninaugural elections would also eliminate the potentially problematic classification of a firm with divergent election results as both treated and untreated. Online appendix figure 8 shows the vote share distribution among inaugural elections. While the discontinuity at the determinative vote share threshold disappears, too few elections remain in order to infer precisely estimated results from the main specification.

I address these concerns in multiple ways. For example, even in the full sample, I retain only inaugural elections at an establishment within a firm so that a particular establishment will never be both treated and untreated. In addition, I estimate alongside the full sample results two other specifications. First, I account for the possibility that pretreatment differences in union penetration across firms affect the impact of subsequent unionization on worker compensation by controlling for the number of previously unionized units at a firm. Doing so allows for the possibility of capturing different-sized effects of union certification according to whether the unionization is new or incremental. Second, I estimate equation (2) on the deficient sample of the first such elections observed at a firm and assess whether the results are broadly consistent with those furnished using the other two approaches.

### B. Effects of Unionization on Worker Compensation

Due to concerns raised in the previous section, level comparisons of outcomes among close union winners and close union winners will not necessarily reflect the causal effect of union certification. Instead, one can analyze the temporal trend in worker compensation before and after union elections. While the levels of preelection average worker compensation are different across treated and untreated firms, the trends are similar. After the election takes place, however, close union winners exhibit a sharp increase in the average worker's total compensation relative to close union losers. Employer contributions to worker pension plans mimic this pattern, suggesting that the rise in compensation at newly certified firms may be attributable to the negotiation of more generous benefit packages by unions.

#### Total worker compensation effects.

After accounting for preelection selection, union certification increases annual average worker compensation by between 7% and 10% ($4,800–$6,900). Figure 2a captures changes in worker compensation over time for both treated and untreated groups that win and lose elections by less than 20% of the vote. Preelection time trends in worker compensation for firms that eventually unionize mirror those of their nonunionizing counterparts, while unionizers experience a relative 10 log point increase in worker compensation following the election. Figure 2b reproduces the same graph for firms whose establishment union elections are decided by less than 15% of the vote. Again, preelection compensation patterns are similar across union winners and losers, while union winners experience approximately a 10 point log point bump in average worker compensation following the election.

Figures 3a (MNE sample) and 3b (Compustat sample) tabulate average changes in pre- and postelection worker compensation by vote share bins (by 5 percentage point bins in the case of figure 3a and by 10 percentage point bins in the case of figure 3b). The left panels show changes in average worker compensation from two years prior to the election to one year prior to the election, while the right panels show changes from one year prior to election to one year after the election. Noticeable jumps at the threshold arise for the postelection changes in worker compensation relative to changes in preelection compensation, where compensation measures appear to be largely continuous about the threshold.

In figures 4a (MNE sample) and 4b (Compustat sample), I repeat this exercise for both the MNE and Compustat samples after transforming the running variable into the margin of victory by vote tally. Here, the vote tally bins are set to a width of one vote in the MNE sample and ten votes in the smaller Compustat sample due to a lack of precision owing to a somewhat deficient sample. Again, the right panels display a 5% to 10% jump in average worker compensation on the union victory side of the 0 margin-of-victory threshold, whereas the left panels appear to be continuous over the same domain. For a more precise characterization of the treatment effect, I analyze the associated regression results of the effects of union certification on worker compensation.

Figure 4.

Change in Average Log Compensation, by Vote Tally

Panel a shows the change in log compensation by union vote tally margins of victory for 827 matched BEA MNE Survey firms and NLRB union election results, and panel b does so for the 163 matched Compustat firms and NLRB union election results. The left sides of panels a and b show the change from two years prior to the election to one year prior to the election, while the right sides show the change from one year prior to the election to one year after the election. The plot displays conditional means and 95% confidence intervals by vote share bins with width one vote (and ten votes).

Figure 4.

Change in Average Log Compensation, by Vote Tally

Panel a shows the change in log compensation by union vote tally margins of victory for 827 matched BEA MNE Survey firms and NLRB union election results, and panel b does so for the 163 matched Compustat firms and NLRB union election results. The left sides of panels a and b show the change from two years prior to the election to one year prior to the election, while the right sides show the change from one year prior to the election to one year after the election. The plot displays conditional means and 95% confidence intervals by vote share bins with width one vote (and ten votes).

Table 3 shows the results of local polynomial regressions (linear and quadratic) that estimate the effect of union representation on the change in average worker compensation at a firm. As in Frandsen (2014), I test for robustness to different definitions of what constitutes a close election. I do so by restricting the bandwidth to a vote share of .20 in the first two columns and .15 in the latter two columns. All of the estimates range from 10 to 13 log points, and nearly all are significant at the 10% or 5% level. In table 4, I rerun the same regressions on specifications using the Imbens and Kalyanaraman (2012) optimal bandwidth and a .1 bandwidth as an additional test for robustness. Again, the estimates are reassuringly consistent with one another, ranging from 11 to 18 log points. I also redo the analysis after restricting the bandwidth to elections whose margins of victory or defeat were no greater than fifteen and ten votes in appendix table 5. Here, the results are qualitatively similar, though they lose significance due to a reduction in sample size and statistical power.

Table 3.
Effect of Unionization on Worker Compensation (close elections)
Dependent Variable(1)(2)(3)(4)
Log compensation 0.134* 0.108** 0.132 0.104*
(0.074) (0.052) (0.087) (0.059)
Observations 401 401 310 310
Log compensation 0.139* 0.122** 0.134 0.115*
(0.073) (0.052) (0.087) (0.059)
$1win$$×$ # unionized −0.008** −0.008** −0.008 −0.008
units $t-1$ (0.003) (0.003) (0.005) (0.005)
Observations 401 401 310 310
Log compensation 0.132 0.113 0.037 0.115
(first election only) (0.103) (0.076) (0.121) (0.089)
Observations 149 149 116 116
Differenced? Yes Yes Yes Yes
Running variable Vote share Vote share Vote share Vote share
Bandwidth .2 .2 .15 .15
Dependent Variable(1)(2)(3)(4)
Log compensation 0.134* 0.108** 0.132 0.104*
(0.074) (0.052) (0.087) (0.059)
Observations 401 401 310 310
Log compensation 0.139* 0.122** 0.134 0.115*
(0.073) (0.052) (0.087) (0.059)
$1win$$×$ # unionized −0.008** −0.008** −0.008 −0.008
units $t-1$ (0.003) (0.003) (0.005) (0.005)
Observations 401 401 310 310
Log compensation 0.132 0.113 0.037 0.115
(first election only) (0.103) (0.076) (0.121) (0.089)
Observations 149 149 116 116
Differenced? Yes Yes Yes Yes
Running variable Vote share Vote share Vote share Vote share
Bandwidth .2 .2 .15 .15

Estimates and robust standard errors are reported for the coefficient on an indicator for a union victory in a local polynomial regression of the dependent variable on an indicator for union victory interacted with a polynomial of the specified degree in the union vote share. The dependent variable in columns 1 to 4 is the observation from the year after the union election minus the observation from the year before the election. All regressions are restricted to union elections receiving at least twenty votes and whose vote shares fall within the specified bandwidth.

*$p<0.10$, **$p<0.05$, and ***$p<0.01$.

Table 4.
Effect of Unionization on Worker Compensation (alternate bandwidths)
Dependent Variable(1)(2)(3)(4)
Log compensation 0.117* 0.116*** 0.180 0.130*
(0.062) (0.040) (0.129) (0.077)
Observations 557 557 214 214
Log compensation 0.131** 0.127*** 0.187** 0.074
(0.062) (0.040) (0.075) (0.065)
$1win$$×$ # unionized −0.009*** −0.009*** −0.014** −0.014**
units $t-1$ (0.002) (0.002) (0.006) (0.006)
Observations 557 557 214 214
Log compensation 0.168* 0.115* 0.206 0.022
(first election only) (0.089) (0.066) (0.202) (0.114)
Observations 219 219 84 84
Differenced? Yes Yes Yes Yes
Running variable Vote share Vote share Vote share Vote share
Bandwidth .32 .32 .1 .1
Dependent Variable(1)(2)(3)(4)
Log compensation 0.117* 0.116*** 0.180 0.130*
(0.062) (0.040) (0.129) (0.077)
Observations 557 557 214 214
Log compensation 0.131** 0.127*** 0.187** 0.074
(0.062) (0.040) (0.075) (0.065)
$1win$$×$ # unionized −0.009*** −0.009*** −0.014** −0.014**
units $t-1$ (0.002) (0.002) (0.006) (0.006)
Observations 557 557 214 214
Log compensation 0.168* 0.115* 0.206 0.022
(first election only) (0.089) (0.066) (0.202) (0.114)
Observations 219 219 84 84
Differenced? Yes Yes Yes Yes
Running variable Vote share Vote share Vote share Vote share
Bandwidth .32 .32 .1 .1

Estimates and robust standard errors are reported for the coefficient on an indicator for a union victory in a local polynomial regression of the dependent variable on an indicator for union victory interacted with a polynomial of the specified degree in the union vote tally or share. The dependent variable in columns 1 to 4 is the observation from the year after the union election minus the observation from the year before the election. All regressions are restricted to union elections whose vote shares fall within the specified bandwidth. In the first two columns, the bandwidth is chosen using the Imbens and Kalyanaraman (2012) procedure.

Table 5.
Effect of Unionization on Worker Compensation: All Elections
Dependent Variable(1)(2)(3)(4)
Log compensation 0.141*** 0.082** 0.149** 0.082**
(MNE sample) (0.052) (0.033) (0.050) (0.033)
Observations 827 827 763 763
Log compensation 0.142* 0.066 0.145* 0.069
(MNE sample)$a$ (0.079) (0.053) (0.085) (0.060)
Observations 245 245 208 208
Log compensation 0.104** 0.075** 0.083** 0.063**
(Compustat sample) (0.049) (0.037) (0.042) (0.031)
Observations 163 163 149 149
Differenced? Yes Yes No No
Control for lagged No No Yes Yes
outcome?
Running variable Vote share Vote share Vote share Vote share
Dependent Variable(1)(2)(3)(4)
Log compensation 0.141*** 0.082** 0.149** 0.082**
(MNE sample) (0.052) (0.033) (0.050) (0.033)
Observations 827 827 763 763
Log compensation 0.142* 0.066 0.145* 0.069
(MNE sample)$a$ (0.079) (0.053) (0.085) (0.060)
Observations 245 245 208 208
Log compensation 0.104** 0.075** 0.083** 0.063**
(Compustat sample) (0.049) (0.037) (0.042) (0.031)
Observations 163 163 149 149
Differenced? Yes Yes No No
Control for lagged No No Yes Yes
outcome?
Running variable Vote share Vote share Vote share Vote share

Estimates and robust standard errors are reported for the coefficient on an indicator for a union victory in a regression of the dependent variable on an indicator for union victory interacted with a polynomial of the specified degree in the union vote share. The dependent variable in columns 1 to 2 subtracts the observation from the year before the election from that of the year after the union election. In columns 3 to 4, preelection values of the dependent variable are used as nonparametric controls.

$a$The sample is restricted to first-ever elections held at an establishment.

Next, I explore whether and the extent to which new unionization at a firm differs from unionization at firms with previously unionized units. If there exists intrafirm pressure to minimize differences in worker compensation across its various establishments, the effect of union elections may then depend on the number of already covered units at the firm. Specifically, in the second rows of both tables 3 and 4, I control for the number of existing unionized units within a firm one year prior to the election. Indeed, the existence of one additional unionized unit at a firm reduces the positive worker compensation effect by 1 percentage point. Because the compensation effects of union elections diminish with each successive covered unit, it can be argued that an incipient rising tide of unionization lifts the compensation of other units within the firm to some degree.26 In the third rows, I attempt to further isolate the impact of new certifications by confining the sample to inaugural union elections held at firms. Though applying this criterion eliminates many elections from the sample, the results are broadly consistent with the previous ones and are marginally significant ($p<0.10$) in the largest subsamples.

Although the modal election is a close one in the data, I also reestimate global polynomial regressions on the entire sample of elections in order to see if the results translate to elections that are not close. This exercise is closer in spirit to the descriptive analysis that motivated the wage analysis, as causal effects are only identified for union elections close to the 50% cutoff. It is possible to extrapolate causal effects away from the cutoff value, though this requires stronger assumptions and more demanding data requirements than can be met in the current context (Angrist & Rokkanen, 2015). Table 5 displays the results of these regressions using the preferred running variable specification of the vote share. The first two columns isolate changes in the average worker compensation variable, while the latter two columns control nonparametrically for the preelection average compensation values. Average worker compensation again increases by 7 to 14 log points (significant at the 5% or 1% level) among all unionizing firms in both samples. Row 2 shows estimates for inaugural elections held at a firm. The point estimates are similar to those produced within the full sample and are marginally significant ($p<0.10$) in two of the specifications.

In appendix table 6, I reestimate the relationship between union certification and average worker compensation after controlling for year effects, the number of previously unionized units, and whether the election-holding plant is located in a right-to-work (rtw) state.27 Unions operating in a right-to-work environment presumably have less bargaining power than do their counterparts in non-right-to-work states since union fees are unenforceable. Therefore, one should expect that right-to-work state unions are less able to win more generous compensation packages for their workers following certification. While rtw effects are negative but small and insignificant in the MNE sample, unionizing firms see anywhere from 55% to the full value of compensation gains wiped out by merit of operating in a right-to-work state in the Compustat sample, with considerably greater precision. These findings provide some suggestive evidence that right-to-work states do limit the ability of unions to win compensation concessions for their workers, though further investigation is merited. Moreover, as with the restricted sample estimates from tables 3 and 4, the presence of one additional unionized unit within a firm reduces the worker compensation effect of successful union election drives by approximately 1 percentage point ($p<0.01$). The estimates of the main effect are again consistent across various specifications and both firm samples, ranging from a 7 to 14 percentage point increase in compensation.

Table 6.
Effect of Unionization on Employer Contributions to Worker Pension Plans
Dependent Variable(1)(2)(3)(4)
Employer pension contributions (victory margin $≤$ 35%) 0.350*** 0.329*** 0.388*** 0.412***
(0.094) (0.089) (0.096) (0.090)
$1win$$×$ right-to-work state  0.052 0.244 0.200
(0.236) (0.245) (0.231)
$1win$$×$ # unionized units $t-1$  0.005 0.001 −0.008
(0.009) (0.013) (0.013)
Observations 237 237 237 237
$R2$ 0.059 0.059 0.235 0.400
Employer pension contributions (full sample) 0.200* 0.230** 0.254** 0.252**
(0.106) (0.092) (0.112) (0.107)
$1win$$×$ right-to-work state  −0.139 0.111 0.071
(0.287) (0.226) (0.212)
$1win$$×$ # unionized units $t-1$  0.004 0.004 0.001
(0.009) (0.016) (0.015)
Observations 260 260 260 260
$R2$ 0.016 0.018 0.216 0.347
Differenced? Yes Yes Yes Yes
Industry FEs No No Yes Yes
Year FEs No No No Yes
Dependent Variable(1)(2)(3)(4)
Employer pension contributions (victory margin $≤$ 35%) 0.350*** 0.329*** 0.388*** 0.412***
(0.094) (0.089) (0.096) (0.090)
$1win$$×$ right-to-work state  0.052 0.244 0.200
(0.236) (0.245) (0.231)
$1win$$×$ # unionized units $t-1$  0.005 0.001 −0.008
(0.009) (0.013) (0.013)
Observations 237 237 237 237
$R2$ 0.059 0.059 0.235 0.400
Employer pension contributions (full sample) 0.200* 0.230** 0.254** 0.252**
(0.106) (0.092) (0.112) (0.107)
$1win$$×$ right-to-work state  −0.139 0.111 0.071
(0.287) (0.226) (0.212)
$1win$$×$ # unionized units $t-1$  0.004 0.004 0.001
(0.009) (0.016) (0.015)
Observations 260 260 260 260
$R2$ 0.016 0.018 0.216 0.347
Differenced? Yes Yes Yes Yes
Industry FEs No No Yes Yes
Year FEs No No No Yes

Estimates and robust standard errors are reported for the coefficient on an indicator for a union victory. All elections received at least twenty votes. The dependent variable is log(employer contributions to per worker pension plans).

#### Effects on employer contributions to worker pension plans.

Past work analyzing firm- and establishment-level union effects have found no positive wage effects. In appendix section A, I replicate these results using the benchmark MNE sample. Since subsequent estimates also reveal that union certification increases worker compensation—the sum of wages and benefits—these two results can coexist only if unions negotiate more generous benefit packages. Thus, I analyze the effects of certification on one salient component of the employee benefit package: employer contributions to worker pension plans.

Due to data limitations—employer contributions data are available for only 260 union election-firm pair matches with the Compustat database—the analysis will resemble that of appendix section A in that it is descriptive only. In the bottom panel of table 6, I analyze the relationship between union victories and changes in employer contributions to worker pension accounts for the full matched sample of firms. The association between unionization status and changes in employer pension contributions is economically large, ranging from 20 to 25 percentage points.

When restricting the sample to union elections decided by fewer than 35% of the vote share, the employer pension contribution effects of union certification are qualitatively similar to those recovered in the unrestricted sample. The top panel of table 6 shows that among all firms, the association between union victories and employer pension contributions ranges from a statistically significant ($p<0.01$) 35 to 41 percentage points.

This 20 to 40 percentage point difference in employer pension contributions amounts to $400 to$750 per worker per year. In light of the $4,800 to$6,900 total compensation increase, these estimates seem plausible. The 2018 BLSs Employer Cost of Employee Compensation Survey reports average fringe benefits of $11.55 per hour across all workers, of which private retirement and savings comprise$1.92 per hour. The difference captures other forms of nonwage compensation, such as health insurance benefits and vacation pay. Similarly, the difference between this study's estimates of the union compensation and pension effects can be explained by increases along other fringe benefit margins or by increases in wages, though mounting evidence suggests that the former plays a more prominent role than does the latter.

## VI. Conclusion

This paper studies the impact of union certification at a firm on worker earnings by comparing outcomes for firms close to the majority rule voting threshold in union representation elections. Nonrandom selection around this pivotal threshold, however, invalidates the classic RDD approach. I circumvent this problem by using the panel nature of the data to control for preelection outcomes and trends, as in Frandsen (2014). After doing so, I obtain results that seem incongruous with prior firm- and establishment-level studies that find no effect of unionization on wages. However, the primary outcome of this study is worker compensation rather than wages. When using this more comprehensive outcome measure, I find that union certifications increase annual average worker compensation by 7% to 10% ($4,800–$6,900) in two independent firm-level data sets. I also replicate the null wage effects of union representation with my data (though with limited precision).

I bolster this analysis by showing that unionizing firms contribute an average of at least 20% more ($400–$750) to their workers' pension accounts following a successful election. While the former finding is novel, the latter result accords with Frandsen and Webb (forthcoming), which shows that collective bargaining agreements increase government contributions to employee pension plans. My results suggest that private sector employees benefit from a similar uptick in employer pension contribution generosity following a union certification.

Taking these treatment effects at face value, I estimate the impact of the private sector deunionization movement on both labor compensation and firm profits. The rate of private sector unionization declined from 16.8% in 1983 to 6.4% in 2016, a year in which the private sector workforce numbered 122 million and the average annual employer cost of compensation for nonunion workers equaled $62,620.28 Based on both the decline in union rates and the estimated union compensation effect,29 12.7 million workers earned$4,400 to $6,300 less in 2016, corresponding to a total loss in compensation of$56 billion to $80 billion, and an increase in firm profits by at least as much depending on the size of union-generated efficiency losses.30 In assessing the extent to which the above results generalize to other firms, however, it is necessary to consider the context in which these effect sizes emerge. This study sample is restricted to a nonrepresentative collection of especially large firms. But there is a positive link between firm size and unionism (Hirsch & Berger, 1984; Hirsch & Addison, 1986; Acs & Audretsch, 1987; Even & Macpherson, 1990; Hollister, 2004), which can be explained by economies of scale in union organizing activity: larger worker pools permit union organizers to recruit employees at a lower cost (Wunnava & Ewing, 1999). Hollister (2004), for example, reports that unionization rates increase monotonically from a low of 5% among firms with fewer than 25 employees to a high of 18% among firms with more than 1,000 employees. Thus, while the firms considered here are uniquely large, they at least represent a population that is perhaps most susceptible to unionization efforts. Empirical evidence further suggests that the union-nonunion wage differential decreases with firm size (Mellow, 1982) as union threat effects, which induce nonunion firms to behave more like unionized ones, are stronger at larger firms, again due to their enhanced susceptibility to unionization. Analogous arguments intimate a parallel relationship between firm size and fringe benefits. Because the benefits' share of total compensation increases with firm size, benefits concessions are also relatively more valuable to workers at smaller firms, ceteris paribus. Indeed, within the current study, the total compensation effect of a union certification for the subsample of smaller firms far exceeds that estimated for the full sample. The two benchmark union election studies that estimate null wage effects of unionization (DiNardo & Lee, 2004; Frandsen, 2014) do so on a sample of establishments affiliated with firms far smaller than those considered in the current sample. Even still, firm-level union wage effects should be bounded above by establishment-level union wage effects. However, the Internal Revenue Service requires that firms distribute benefits to all similarly situated employees within a firm in a nondiscriminatory manner, lest they forfeit the tax-exempt status of self-insured health plans and deferred tax treatment of employer pensions (Even & Macpherson, 1994; Beam & McFadden, 2001). Thus, any unionization-induced increase in fringe benefits at an establishment will likely be propagated across all other establishments of the firm so that the union wage and union fringe effects among the larger firms in the current setting provide a lower bound for the estimands of prior union election studies. Not to be lost is the implied importance of this spillover channel in generating these firm-wide compensation gains, as they are triggered by an incongruously small number of votes. Roughly 39,000 pro-union votes (in the MNE sample) increase economy-wide employee compensation by$113 billion,31 which amounts to a staggering $2.9 million per majority vote. Given the large size of the firms analyzed in this study, however, the windfall accruing to firms through preferred tax treatment on fringe benefits guaranteed by the neutral provision of such benefits lends plausibility to these results. These estimates also supplement recent work by Farber et al. (2018) by suggesting that if unionization reduces income inequality, it does so by boosting, rather than merely reallocating, compensation across workers. Thus, this study reconciles textbook theoretical predictions of positive union earnings premiums with the failure of the union elections literature to show positive union wage effects by presenting new empirical evidence that the union premium is in fact positive so long as the definition of worker compensation includes benefits. Frandsen (2014) decomposes union earnings into a price and composition effect, finding no price effect along with a negative composition effect of unions on wages. In contrast, I estimate a positive combined effect of union certifications on benefits plus wages. This suggests that the estimated 7% to 10% compensation increase is a lower bound on the price effect of certification as I cannot disentangle the negative composition effect from the total observed effect with my data. Because of the puzzling nature of the results, it is worth taking a broader view of how firms susceptible to unionization differ from their counterparts. Freeman (1981) shows that trade unionism predicts a greater fringe benefit share of compensation.32 The primary justification is that unions, as political institutions, must reflect the preferences of the majority of workers whom they represent. If there exists a contingent of older, less mobile workers for whom fringe benefits are more valuable,33 the majority (or median) preference will shift toward a compensation package with more generous fringe benefits (Abowd & Farber, 1982; Hirsch & Berger, 1984). This stands in contrast to the outcome that would prevail in a competitive market, whereby the compensation package is instead determined by the marginal employee. This view is further reinforced by Freeman (1980a), which demonstrates that unionism increases job attachment through higher tenure and lower quit rates, improving the likelihood that workers will receive deferred fringe benefits, such as pension and life insurance plans. Unionized workers in turn are especially willing to forgo higher wages in exchange for more generous deferred benefits. That employer contributions to pension plans rise precipitously following a successful union election in the current study appears to vindicate this prediction. The paper's results should also be considered a substantiation of the conclusion emerging from the pioneering work of Freeman (1981), which, in a cross-sectional study of establishments, finds, “The union fringe effect exceeds, in percentage terms, the union wage effect and is sufficiently large to suggest that standard union wage studies understate the union effect on total compensation.” More broadly, this study underscores the importance of considering total compensation effects in favor of wage effects when evaluating the impact of various economic policies. To the extent that employers respond to regulations on the benefits margin, the current paradigm may understate or overstate the true earnings effect. Taking a more holistic approach to measuring worker compensation may yet generate new insights on issues that lie at the core of labor economics, such as the gender pay gap, the price effects of minimum wage regulation, and Mincerian estimates of the effect of education on earnings. ## Notes 2 See section 105 of the Internal Revenue Code for more details. 3 Ruback and Zimmerman (1984) were the first to use an event-study design to estimate union effects on firm equity values, but their underpowered sample precluded precise inference. 4 In 2016 dollars, the total decline in equity is$29.45 million, and the average firm in Lee and Mas (2012) has 3,530 employees.

5

These calculations use average worker compensation from the Compustat sample in order to maintain consistency with Lee and Mas (2012), who use the same database.

6

The description of the union election process in this section is based on Frandsen (2014).

7

These cases are rare as employers generally resist organization drives (Kleiner, 2001).

8

These steps follow NLRB (2010).

9

See Lee (2008) for a proof of this assertion.

10

These disputes are fairly commonplace as well, occurring in over 21% of union representation drives between 1999 and 2004 (Ferguson, 2008).

11

Additionally, all vote tabulations and election results from 2001 onward are archived on the NLRB website: https://www.nlrb.gov/reports-guidance/reports/electionreports.

12

While nearly 90,000 NLRB union certification elections were held over the study period, the election summary statistics in table 1 reflect only those taking place at firms in either the MNE or Compustat samples. Refer to online appendix C for the underlying details on the outcomes of the process through which these union elections are matched with their enveloping firms.

13

Summary statistics for 261 union elections, corresponding to an auxiliary sample in which data on employer pension contributions are available, are also provided in table 1.

14

The BEA MNE Survey also collects data on the operations of foreign affiliates associated with the U.S.-based multinational firms. However, in this study, I use data on the U.S. parent companies only, which constitute the U.S. domestic operations of multinational enterprises. Other activities tracked include sales by type and destination, value added, employment and employee compensation, U.S. trade in goods, and research and development.

16

In fact, pension plan data are available for an additional 98 firms beyond those for which employee compensation data are provided.

17

Duplicate observations across databases were removed.

18

While nearly 89% of the sample MNE firms and just over 95% of the sample Compustat firms possess more than 1,000 employees, only 0.2% of all U.S. firms employ more than 1,000 employees (Census Bureau's Business Dynamics Statistics, 1983–2009).

19

This difference disappears when only close union winners and losers are considered.

20

Note, however, that part of the difference in average earnings may also reflect the fact that larger, more prominent U.S. companies pay better wages than the average U.S. firm.

21

Additionally, 163 union elections were matched to a firm in the Compustat database, and 414 union elections were matched to a firm in the BEA MNE Benchmark Survey.

22

More details on the matching procedure are included in appendix D.

23

Identification of union election effects in this section is based on Frandsen (2014).

24

Because the McCrary test may perform poorly when the running variable is discrete, I also implement the Frandsen (2017) analog of the McCrary (2008) test.

25

The discontinuity in the MNE vote share is made even more salient when the vote share is partitioned by fifty bins rather than twenty, as in appendix figure 1.

26

Private sector unionization, however, declined by more than half between 1983 to 2009, from 16.8% to 7.2%, and fell further to 6.4% in 2016. Thus, the direction of intrafirm union spillovers should have reversed dramatically over the study period and beyond.

27

Elections conducted in right-to-work states account for 36% of all sample observations.

28

This figure is derived from the 2016 BLS National Compensation Survey.

29

I also assume that compensation effects are symmetric.

30

This calculation does not consider any union disemployment effects, which have emerged in some earlier studies (Leonard, 1992; Long, 1993; Frandsen, 2014; Sojourner et al., 2015).

31

7% compensation increase $×$ \$70,000/worker-year $×$ 27,892 workers/firm $×$ 827 firms.

32

Appendix table 7 shows that a similar relationship holds with this study sample.

33

Nealey (1963) shows that older workers prefer fringes to wages, relative to younger ones.

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## Author notes

The views expressed in this paper are solely my own and do not necessarily reflect the views of the Bureau of Economic Analysis. I thank Abe Dunn, Jed DeVaro, and various other seminar participants for their insightful comments.

A supplemental appendix is available online at http://www.mitpressjournals.org/doi/suppl/10.1162/rest_a_00803.