Can Displaced Labor Be Retrained? Evidence from Quasi-Random

Can Displaced Labor Be Retrained? Evidence from

Quasi-Random Assignment to Trade Adjustment Assistance

∗

Benjamin G. Hyman

University of Chicago

This Draft: November 20, 2018

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Abstract

The extent to which workers adjust to labor market disruptions in light of increasing

pressure from trade and automation commands widespread concern. Yet little is known

about efforts that deliberately target the adjustment process. This project studies 20 years

of worker-level earnings and re-employment responses to Trade Adjustment Assistance

(TAA)—a large social insurance program that couples retraining incentives with extended

unemployment insurance (UI) for displaced workers. I estimate causal effects from the

quasi-random assignment of TAA cases to investigators of varying approval leniencies.

Using employer-employee matched Census data on 300,000 workers, I ﬁnd TAA-approved

workers have ∼$50,000 greater cumulative earnings ten years out—driven by both higher

incomes and greater labor force participation. Yet annual returns fully depreciate over the

same period. In the most disrupted regions, workers are more likely to switch industries

and move to labor markets with better opportunities in response to TAA. Combined with

evidence that sustained returns are delivered by training rather than UI transfers, the results

imply a potentially important role for human capital in overcoming adjustment frictions.

∗

I am deeply indebted to Gilles Duranton, Fernando Ferreira, Jessie Handbury, Ann Harrison, and Ben Keys for extensive

advising on this project. I thank David Atkin, David Autor, Anna Cororaton, Matt Davis, Anthony DeFusco, Deeksha Gupta,

Erik Hurst, Bob Inman, Illenin Kondo, Jake Krimmel, Ben Lockwood, Ioana Marinescu, Magne Mogstad, Ryan Monarch, Matt

Notowidigdo, Justin Pierce, Todd Sinai, Boris Vabson, Chris Walters, Maisy Wong, and seminar participants at the IADB,

FRBNY, Johns Hopkins SAIS, NBER Trade and Labor Markets, NBER Labor Studies, UC-Berkeley, UChicago, UChicago-Booth,

USC-Price, and UT-Austin McCombs for helpful comments. I am particularly grateful to Ryan Monarch, Jooyoun Park, and

Jagadeesh Sivadasan for sharing their ﬁrm-matching code, and Brian Kovak for additional take-up data. I acknowledge

generous ﬁnancial support from the Ewing Marion Kauffman Foundation Dissertation Fellowship, and the Wharton Mack

Institute for Innovation. This research uses data from the Census Bureau’s Longitudinal Employer Household Dynamics

Program, which was partially supported by National Science Foundation Grants: SES-9978093, SES-0339191 and ITR-0427889;

National Institute on Aging Grant AG018854; and grants from the Alfred P. Sloan Foundation. Support for this research at

the Suitland RDC from NSF (ITR-0426889) is also gratefully acknowledged. All results have been reviewed to ensure that no

conﬁdential information is disclosed. Research results and conclusions expressed are those of the author and do not reﬂect the

views of the Census Bureau. All errors are my own. Email: [email protected].

1 Introduction

Between 2000 and 2016, the US shed approximately 6 million manufacturing jobs, resulting in the lowest

level of manufacturing employment since the onset of World War II (BLS, 2017).

Strikingly, this decline

contrasted with record revenue growth in both manufacturing and non-manufacturing industries over

the same period (see Figure 1). In light of increasing pressure from trade and automation, are today’s

workers able to adjust to labor market disruptions as they have in the past, or do frictions in the

adjustment process imply a greater role for policy in targeting those displaced?

While trade economists have shown that removing import barriers can increase growth and

consumer welfare through specialization, lower goods prices, and higher variety,

less attention had

been given to adverse consequences for labor because imports from low-wage countries were relatively

inconsequential until the 1990s (Autor et al., 2016). Not robustly detected in the data, the implication was

that growing industries could indeed absorb and offset declining earnings among displaced workers

with little friction.

More recently however, inﬂuential papers in empirical trade and labor economics

have documented that displaced workers may remain persistently underemployed and underpaid (with

respect to prior earnings) years beyond their initial job separation (Bartik A., 2017; Lachowksa et al., 2017;

Pierce and Schott, 2016; Flaaen et al., 2016; Autor et al., 2014, 2013; Autor and Dorn, 2013; Harrison and

McMillan, 2011).

The unusual speed and persistence of these structural changes has generated equal

concern about how future generations will adapt to work in a rapidly automating economy.

Despite widespread attention, remarkably little is know about whether the US’s largest and longest

standing incentive program for retraining displaced workers—the Department of Labor’s 1974 Trade

Adjustment Assistance (TAA) program—is a necessary, effective, or efﬁcient means to accelerate

adjustment. This main goal of this paper is to provide large-sample empirical estimates of the causal

effects of TAA on three labor market outcomes: earnings, employment, and mobility. Credible parameter

estimates of these effects have historically been complicated by two factors: (1) A lack of detailed

worker-level data to track TAA participants before and after displacement events across employers; (2)

Pierce and Schott (2016) highlight that the recent manufacturing decline contrasts with a stable employment trend which

had varied around 18 million jobs from 1965 until the accession of China to the World Trade Organization (WTO) in 2001.

Recent work by Fajgelbaum and Khandelwal (2016) further suggests low-income workers have the most to gain from trade,

as they bear a disproportionate incidence of lower consumer prices due to a higher propensity to consume tradable goods.

Ricardian trade models conventionally assume displaced workers either adjust instantaneously to newly expanding

sectors (i.e. labor is perfectly mobile), or are compensated by redistributive transfers that preserve trade’s Pareto-improving

qualities. The latter relies on the notion of “Kaldor-Hicks Efﬁciency” (Kaldor, 1939; Hicks, 1939), which relaxes Pareto

assumptions such that efﬁcient trade need only require that losing production factors be hypothetically compensatable by

winning factors. This allows agnosticism as to the effectiveness of the redistribution itself—the subject of the current paper.

Feenstra et al. (2017) and Feenstra and Sasahara (2017) ﬁnd that manufacturing job losses are offset by service job growth,

however these papers do not address distributional consequences which can persist despite aggregate gains.

For example, 1.3 million truck drivers are expected to have to compete with the emergence of self-driving vehicle

technology by 2026 (CEA, 2016).

Confounding factors correlated with qualifying for TAA, particularly pre-determined skills and trends

associated with tradable-good production and training take-up—selection biases which preclude reliable

estimates of the program’s effects. In this paper, I employ a quasi-experimental research design that

builds on the rapidly maturing “examiner” literature to circumvent these endogeneity concerns in a

two-stage least squares (2SLS) setting.

I ﬁrst assemble a new dataset combining restricted-use administrative data from the US Census

Bureau’s Longitudinal Employer-Household Dynamics (LEHD) program with the universe of TAA

winning and losing petitions (applications) attained through FOIA requests at the US Department of

Labor (USDOL). This merger allows me to track approximately 300,000 displaced workers as they move

in and out of unemployment status and across employers of diverse industries and regions, both before

and after their initial job separation. Critically, the USDOL assigns TAA petitions to case investigators

tasked with determining whether applicants were laid off by companies whose decline in production

(sales) was due to increased imports or offshoring—an adjudication of the ﬁrm’s trade exposure or

“tradability” status. This institutional feature of TAA effectively assigns two otherwise identical worker

cohorts displaced from the same industry, different approval probabilities based on whether their case

is directed to a more lenient versus strict investigator. If assigned to more lenient investigators, displaced

workers have a higher likelihood of receiving TAA beneﬁts, amounting on average to $10,000/year for

two years of training and $15,000/year of extended unemployment insurance (UI) while training.

I ﬁnd evidence of large initial returns to TAA. Workers inferred to take up beneﬁts forego roughly

$10,000 in income while training, yet ten years later have approximately $50,000 higher cumulative

earnings relative to all-else-equal workers that do not retrain. I estimate that 33% of these returns

are driven by higher wages—a sizable share which suggests that TAA-trained workers are not only

compensated through greater labor force participation or higher priority in job queues. Rather, TAA

workers also appear to be paid a premium for their newly acquired human capital. But these large

relative gains also decay over time, such that annual incomes among TAA and non-TAA workers fully

converge after ten years. In conjunction with two additional pieces of evidence—that TAA has no effect

on formal education, and diminishing returns are restricted to states with low training durations—I

attribute this depreciation to short-run demanded skills becoming obsolete (consistent with rapid

Recent examples of such examiner designs include Dobbie and Song (2015), who use the random assignment of

bankruptcy judges to establish the causal effects of consumer bankruptcy insurance on debtor outcomes; Autor et al. (2015),

who study the welfare impact of disability beneﬁts in Norway; and Mueller-Smith (2015), who studies the impacts of

incarceration. The original idea to exploit judge randomization as a causal design can be attributed to Kling (2006), and the

ﬁrst quasi-experimental examiner design can be attributed to Doyle (2008)

While this design is well-equipped to estimate an important adjustment parameter with respect to training, the TAA

treatment effect (estimated here using an intent-to-treat framework) should be thought of as just one input into a richer trade

model characterizing the full efﬁciency and distributional consequences of trade liberalization.

skill-biased technological change or an overall declining labor share).

Indeed, 62% of TAA training

programs confer vocational degrees with shorter program lengths than typical community college or

4-year college degrees which have been shown to have durable earnings returns (Card (2001); Kane and

Rouse (1995)).

While these results provide strong evidence that overall earnings returns to TAA are largely positive,

government intervention in the adjustment process is only warranted economically in the presence of

market failures or if redistribution is socially desirable.

While human capital theory suggests that wage

differentials across occupations should provide ample incentives for workers and ﬁrms to privately

undertake skill upgrading (Becker, 1964), laid off machine operators in Detroit’s automobile sector

may face a variety of frictions that prevent them from acquiring productive employment in expanding

sectors such as robotics occupations in Pittsburgh’s burgeoning 3D-printing industry. Among several

possible barriers to adjustment, these frictions may be spatial or industrial—high mobility costs across

labor markets and industries stagnate worker wages in trade-afﬂicted labor markets (Bartik A., 2017;

Yagan, 2014; Kline and Moretti, 2013; Blanchard and Katz, 1992); informational—search costs result

in job mismatch after displacement (Moretensen and Pissarides, 1994); ﬁnancial—liquidity constraints

preclude the necessary investments in retraining and education required for work in the modern

economy (Lochner and Monge-Naranjo, 2011); or behavioral—workers may be “present-biased” or make

forecasting errors about the future viability of their local industries (Augenblick et al., 2015).

To unpack which frictions underlie the main effects (if any), I conduct a variety of empirical tests

exploiting the rich heterogeneity of the administrative data to identify potential mechanisms. I ﬁnd

strongest support for spatial and industrial adjustment frictions. Merging county-level Bureau of Labor

Statistics (BLS) unemployment rate data to the LEHD panel, I deﬁne “high” and “low” shock severity

regions based on whether the county in which a TAA-qualiﬁed worker was displaced was above or

below median unemployment in their quarter of separation. I ﬁnd that workers in highly disrupted

regions are more likely to switch both industries and commuting zones (a now widely used geographic

measure of local labor markets) in response to training. Workers are approximately 20 percentage points

more likely to move commuting zones and 28 percentage points more likely to switch industries (at the

2-digit North American Industrial Classiﬁcation System (NAICS) level), with respect to the location and

industry of their pre-layoff employer. Lastly, I ﬁnd no evidence that TAA subsidies lead to deferred job

search, which suggests that effects are more likely due to the training itself and an expansion of potential

ﬁrm matches outside of their trade-shocked region, rather than relieving liquidity or search constraints.

For a discussion of the potential determinants of the declining labor share in the United States, see Autor et al. (2017).

There are arguably other less distortive ways to achieve the latter redistributive goal. See for example recent work by Lyon

and Waugh (2017), who consider optimal progressive taxation schemes to redistribute the gains from trade.

While the paper’s identiﬁcation strategy provides robust evidence of positive earnings returns and

higher mobility associated with TAA, this does not inform us about the cost-effectiveness of the program.

Toward this second end, I compare the ten year stream of estimated TAA differential earnings returns as

beneﬁts, with average TAA expenditures on training, extended UI, and foregone earnings while training,

as costs. I estimate an internal rate of return (IRR) to TAA of between 0.0% and 9.1%, which I interpret

as a lower bound for two reasons. First, earnings returns are calculated from an intent-to-treat (ITT)

estimator which likely understates beneﬁts due to imperfect compliance with the treatment (i.e. partial

take-up of TAA attenuates earnings estimates toward zero and understate the treatment-on-treated

(TOT) effect of interest). Second, TAA may induce worker substitution away from other costly social

insurance programs such as disability insurance (DI), which would further understate program costs.

One important caveat however, is that positive earnings returns are estimated from a local average

treatment effect (LATE) that does not capture the fact that ﬁrms may be incentivized to lay off additional

workers after learning of their TAA eligibility status. Nevertheless, back-of-the-envelope calculations

show that these are unlikely to outweigh potentially much larger downward pressures.

Overall, this paper provides new quasi-experimental evidence that earnings returns from

trade-adjustment targeting via retraining may be larger and more effective than previously thought.

More work is needed however, to fully understand the extent to which such targeting alleviates

aggregate worker adjustment barriers, and to decompose the relative roles of training and UI in its

success. Despite some noteworthy inefﬁciencies, TAA may serve as an important tag for redistributing

the growth from trade. However, whether these results can be extrapolated to trade and automation

pressures faced by future workers remains an open question.

1.1 Related Literature

While this paper is one of the ﬁrst to empirically estimate the effects of TAA on worker outcomes,

the study builds on a long history of scholarship in labor economics, trade, and public economics.

Particularly, this analysis is positioned at the intersection of three literatures: (1) The impact of worker

displacement and trade on inequality; (2) The effects of job training on earnings and human capital

accumulation; (3) The role of local labor market and occupational mobility frictions in earnings growth.

Starting with displacement and inequality, this paper most directly follows the work of Autor et

al. (2016), who study long run earnings adjustment patterns of workers exposed to Chinese import

competition using administrative Social Security Administration (SSA) data. The authors ﬁnd long-run

negative effects from trade, and show that trade-affected workers take up disability insurance (DI)

Autor et al. (2014) ﬁnd that DI is in fact the predominant margin through which workers adjust to trade shocks.

rather than trade adjustment assistance to insure themselves against these shocks.

Recently, other

scholars have also studied displacement and inequality through the lenses of trade (Pierce and Schott,

2016; Ebenstein et al., 2014; Autor et al., 2013; Amiti and Davis, 2011; Harrison and McMillan, 2011;

Kletzer, 2004), technology and automation (Autor et al., 2013; Acemoglu and Autor, 2011; Goldin and

Katz, 2009), business cycle ﬂuctuations (Lachowksa et al. (2017), Von Wachter et al. (2009)), and reasons

for separation (Flaaen et al., 2016). One additional catalyst for renewed interest in this topic has been

greater availability of administrative datasets which facilitate more precise estimates of heterogeneous

responses to different types of separation events.

Work on displacement has also been linked to a longer tradition of scholarship on job training, which

has been the source of several methodological advancements in labor economics and debate surrounding

the econometrics of program evaluation. Early literature focused on either model-based econometric

selection correction methods (Heckman, 1976) or difference-in-differences estimators (Ashenfelter

(1978)) to address a number of endogeneity concerns, and found little to no effects of job training on

worker outcomes. Ashenfelter and Card (1985) however, showed that difference-in-differences estimates

were sensitive to the control groups used, while LaLonde (1986) demonstrated that experimental results

did not match non-randomized econometric studies. This was followed by rapid advancement in the

development of matching estimators and propensity score methods (Heckman et al., 1996, 1997), and

continued debate over how to resolve the critique of nonexperimental approaches to estimation.

In their 1999 handbook chapter, Heckman, LaLonde, and Smith (1999) bridge the debate by calling for

better data and experimental evidence when possible. Subsequently, in a meta-analysis of 97 job training

program evaluations from 1995 to 2007 that more frequently employ experimental variation and higher

quality data, Card et al. (2010) follow up on prior estimates with a similarly titled handbook chapter, and

conclude that ”...training programmes are associated with positive medium-term impacts, although in

the short term they often appear ineffective.” When converted to standardized effect sizes, this paper’s

employment results fall near the middle of those effect sizes classiﬁed as “signiﬁcantly positive” in the

Card et al. (2010) study: 0.25 (β=0.1/sd=0.4), compared to the Card et al. (2010) median of 0.21.

While TAA is a sizable training program, there is a surprising dearth of evidence on its empirical

effects on workers.

One notable exception is a recent study by Mathematica Policy Research authors

One can compare these persistent adverse effects form import competition to the relative returns to retraining through

TAA. Importantly however, Autor et al. (2016) consider the joint effect on workers who may see reduced earnings or hours on

the intensive margin, as well as workers who are displaced (the unit of analysis in this paper). These sample differences thus

present important caveats when making direct estimate comparisons.

Dehejia and Wahba (1999) ﬁrst indicated that LaLonde’s critique could be addressed using propensity score methods, but

later work by Smith and Todd (2001) showed the limitations of this approach.

Notable exceptions include Feenstra and Lewis (1994), who provide a strong theoretical foundation for considering the role

of adjustment assistance in the context of imperfect mobility. Monarch et al. (2017) and Kondo (2013) also use TAA-approved

plants as a lever to study the effects of offshoring on ﬁrms and displacement multipliers respectively.

Schochet et al. (2012), who evaluate the effects of TAA by comparing program enrollees with a

propensity-score matched sample of UI claimants that do not take up TAA. The authors ﬁnd a mostly

negative result, concluding that “...impacts of TAA on engagement in any productive activity were

small.” However, they are also very careful to note two important caveats in interpreting their effects.

First, the sample frame used in their study included manufacturing workers who were laid off just before

a large economic downturn—sampled between 2005 to 2006. Since TAA trainees enroll for up to 2 to 3

years and the study only tracked workers for 4 years after enrollment, TAA workers would have entered

a more dismal labor market relative to matched UI claimants who may have been reemployed during a

more robust economy after exhausting short-run UI beneﬁts.

Second, and consistent with conclusions

from the propensity score literature which calls for a large number of observables for internal validity

(Todd (2010)), the authors recognize that unobserved heterogeneity may result in differently selected

samples across the two groups. In this paper, I contribute direct causal estimates of how training

programs affect worker mobility across local labor markets and industries.

The third literature relates to imperfect spatial and industrial mobility. Pioneering work by Blanchard

and Katz (1992) highlighted the empirical importance of worker mobility as an equilibrating factor across

differently shocked labor markets, and has been by studies on the effects of mobility constraints on

workers. These questions have been studied in the context of migratory insurance during recessions

(Yagan (2014)), responses to trade shocks ((Dix-Carneiro and Kovak, 2017; Bartik A., 2017; Kovak et

al., 2017)), and in the context of place-based policies and taxation (Serrato-Su

arez and Zidar (2016),

Kline and Moretti (2014, 2013)). In a theoretical paper analyzing trade compensation in a general

equilibrium framework, Feenstra and Lewis (1994) build on the work of Dixit and Norman (1986) and

show that redistributive compensation from levying taxes on winning factors are more likely to result in

a Pareto-improving allocation if combined with mobility subsidies to overcome adjustment frictions. In

these and other papers, relaxing the benchmark of a perfectly elastic labor supply across regions, sectors,

and occupations, generate myriad frictions which are only now beginning to be tested empirically.

The rest of the paper proceeds as follows. Section 2 provides institutional background on Trade

Adjustment Assistance, worker eligibility for beneﬁts, and the composition of training programs taken

up. In Section 3, I discuss the main administrative data sources used, matching procedures and sample

restrictions. Section 4 outlines the investigator leniency identiﬁcation strategy and estimating equations.

Section 5 presents the main results on worker-level outcomes, and heterogeneous mobility and training

intensity effects. I contextualize these results in a cost-beneﬁt analysis in Section 6, presenting the internal

rate of return of TAA and sensitivity to assumptions. Section 7 concludes.

Standard UI beneﬁts typically last for 26 weeks, however during the Great Recession both generosity and duration were

greatly expanded.

2 Trade Adjustment Assistance

When considerations of national policy make it desirable to avoid higher tariffs, those injured by

that competition should not be required to bear the full brunt of the impact. Rather, the burden

of economic adjustment should be borne in part by the Federal Government... But the accent is

on “adjustment” more than “assistance”. Through trade adjustment prompt and effective help can

be given to those suffering genuine hardship in adjusting to import competition, moving men and

resources of uneconomic production into efﬁcient production and competitive positions...

—John F. Kennedy, Congressional address on the 1962 Trade Expansion Act (originally cited by Kondo (2013))

2.1 Institutional Background

US Trade Adjustment Assistance (TAA) is a federal transfer program established under the 1962 Trade

Expansion Act which provides assistance to workers “who lose their jobs or whose hours of work and

wages are reduced as a result of increased imports or shifts in production out of the United States.”

The program was established during the Kennedy Round of the General Agreement on Tariffs and Trade

(GATT), and sought to couple unprecedented trade liberalization (part of a more widespread post-war

trade integration effort) with adjustment insurance for adversely affected US workers.

The current program is governed by the 1974 Trade Act, and was amended several times throughout

the 1980s altering the generosity of its beneﬁts. In 1993, TAA was expanded to add additional coverage

for workers directly affected by the North American Free Trade Agreement (NAFTA-TAA), however

this provision was subsequently repealed in the Trade Act of 2002. Since 2002 however, TAA beneﬁts

have remained relatively stable in expenditure terms. In ﬁscal year 2010, nearly $1 billion in annual cash

transfers were appropriated to subsidize an estimated 230,000 qualiﬁed workers to enroll in retraining

programs after trade-related layoffs.

While TAA contains several program components, its primary

beneﬁt is coverage of training costs for every year a qualiﬁed worker is retraining, up to a statutory

maximum of three years. Median annual coverage from 2001 to 2016 was $7,500/recipient-year,

including up to two years for “basic” retraining, and an additional year for “remedial” training (if

deemed necessary) or “completion” training for workers who are close to completing a credentialed

curriculum but have exhausted basic beneﬁts.

Recipients are also entitled to expanded unemployment insurance (UI) beneﬁts while training (called

“Trade Readjustment Allowances” (TRA)), conditional on providing regular proof of training enrollment.

Institutional details in this section build on those presented in Monarch et al. (2017) and Kondo (2013), and are amended

based on secondary sources and interviews with Ofﬁce of Trade Adjustment Assistance ofﬁcials.

Department of Labor, Employment and Training Administration. https://www.doleta.gov/tradeact/taa_wdp.cfm

Department of Labor, Employment and Training Administration. https://www.doleta.gov/tradeact/factsheet.cf.

This conditional incentive design is distinct from standard UI, in that it intends to overcome moral

hazard concerns associated with search disincentives, imposing at least minimal “search effort” through

job training.

Workers are eligible for extended UI for up to three years, including the standard initial

26-week UI duration which is most common across US states. Median receipts on extended UI roughly

equaled $15,000/recipient-year from 2001 to 2016, roughly double the $7,500/recipient-year median

offered for training.

Lastly, TAA covers 90% of job search and relocation costs, yet these comprise

less than 0.1% of total spending, and are hence given little attention throughout the analysis.

TAA funds are allocated via state transfers to Cooperating State Agencies (CSAs) from the Federal

Unemployment Beneﬁts and Allowances (FUBA) account. Once workers are approved for TAA, state

career centers (e.g. American Job Centers, One-Stop Career Centers) guide workers to potential training

program matches based on prior experience. However, workers ultimately have choice over where

to train. Once they have demonstrated proof of enrollment, both training subsidies and regular TRA

payments are administered through local state career centers, where workers recoup paychecks.

2.2 Worker Eligibility

To receive TAA beneﬁts, workers (or their surrogates) must ﬁle petitions at the USDOL within one year

of their trade-related separation from a given employer. Filers may include groups of three or more

workers (38% of total ﬁlers), companies ﬁling on behalf of laid off workers (36%), labor unions (13%),

or state career centers (13%).

From 1974 to 2016, the USDOL received petitions covering an estimated

8.2 million workers, of which approximately 63% were approved for TAA (see Figure 2). Petitions were

ﬁled on behalf of workers from more than 40,000 unique plants, and the number of approved applicants

began to outstrip denied applicants after the passage of NAFTA.

Once a petition is ﬁled at USDOL, Ofﬁce of Trade Adjustment Assistance supervisors (“certifying

ofﬁcers”) assign petitions to case investigators working from the Washington D.C. headquarters.

(This

assignment process is described in greater detail in the identiﬁcation strategy in Section 4.) These

investigators are tasked with subjectively determining whether applicants were laid off by companies

whose decline in production (sales) was due to increased imports or outsourcing, and have subpoena

power to request conﬁdential information from any given ﬁrm or plant to assess whether its separated

Workers near retirement age however, may not ﬁnd time and effort costs of training to be a high trade-off for extended UI.

The extent of this support varies formulaicly by each state’s initial UI generosity. Data used for this calculation comes

from the Trade Act Participant Report (TAPR) from 2001 to 2016. See Appendix B.5 for more details.

TAA has also been experimenting with wage insurance to bridge the income gap for older workers, however this program

(know as Alternative or Reemployment TAA) is beyond the scope of the current project.

Percentages from author calculations based on USDOL petition data, 1974 - 2016.

Figure 2 also demonstrates a countercyclical ﬁling pattern. However this may be unsurprising, as ﬁrms have been shown

to make structural adjustments precisely during recessions (Aghion et al., 2005).

The short TAA petition form can be found here: https://www.doleta.gov/tradeact/docs/RevisedPetition.pdf

workers qualify for TAA.

To qualify, investigators look for one of three criteria:

(1) Direct reduction in sales from import competition

(2) Shifts in production outside the US

(3) Upstream supplier or downstream client of ﬁrms affected by (1) or (2)

Importantly, once investigators certify a petition associated with a given plant, all workers displaced

from that plant within a speciﬁed 3-year eligibility window automatically qualify for TAA, despite who

ﬁles. The timeline below illustrates this point, and shows which displaced workers are eligible for TAA

based on a statutory window around the petition determination date (event time τ = 0). When a petition

is ﬁled, investigators record the “impact date” as the date a worker-cohort was laid off due to a trade

event, which may not exceed one year prior to when the petition is ﬁled. The “expiry date” marks the last

day a worker can be laid off and still receive beneﬁts—statutorily two years after the petition decision.

−τ

−1

0 2

TAA Eligibility Window

(displaced workers)

Analysis

Sample

Distorted

Firing

Incentives

τ = −1: TAA “Impact Date” (≈ Displacement Date)

τ = 0: TAA Determination Date (Approve/Deny)

τ = 2: TAA Eligibility Expiry Date

In corresponding Census microdata, I thus identify my sample as all “displaced” workers that

move from positive to non-positive earnings at a petition-associated plant, within the TAA eligibility

window.

One unintended consequence of this eligibility design is that the plant itself may become

aware of its workers’ TAA approval status after the decision is made public at τ = 0. If so, ﬁrms

with union-represented workforces or those located in “company-towns” may have an incentive to ﬁre

additional workers who were originally retained after the ﬁrst wave of layoffs, with the knowledge that

these workers will be compensated.

Because retained workers are presumably selected for higher

productivity and would only be laid off if approved for TAA, this could contaminate the treatment group

Investigators do this by issuing Conﬁdential Data Requests: https://www.doleta.gov/tradeact/pdf/CDR_Service.pdf,

and typically arrive at a determination decision within 60 days.

Upstream suppliers and downstream clients have qualiﬁed since 2002.

The main results are robust to a number of sensitivity samples that use alternative deﬁnitions of displacement that more

closely follow the “mass layoff” literature. These are discussed further in the sample restrictions outlined in Section 3.

Whether the motive is proﬁt or non-proﬁt rooted, as noted above, most petitions are ﬁled by companies instituting layoffs

rather than workers or unions.

and bias earnings estimates upwards. I thus only include workers laid off in the one year prior to the

petition decision. Despite this relatively conservative condition, I am still able to identify a ﬁnal sample

of roughly 300,000 displaced workers after sampling restrictions.

While the treatment is effectively

at the plant-level, this does not guarantee that information about TAA eligibility disseminates to all

qualiﬁed workers. However, it does allow for the estimation of an intent-to-treat (ITT) estimator which

reﬂects the effects of qualifying for TAA despite potential program shortcomings such as information

asymmetries. Indeed, Schochet et al. (2012) estimate that 25-45% of workers offered TAA beneﬁts

actually take up the program. In combination with the additional restriction above to preclude perverse

incentive problems, these are important limitations when interpreting local average treatment effects

and weighing program beneﬁts against costs.

2.3 TAA Training Programs

The USDOL classiﬁes training by three main categories: occupational (vocational, trade schools,

community college, associates degree, etc.), remedial (elementary proﬁciency), and work-based training

(including on-the-job, customized, and apprentice training at the ﬁrm from which the worker separated

if rehiring in a different occupation post-training).

According to TAA performance data from 2000

to 2016, 62% of TAA workers enrolled in occupational training programs, 18% in community college

and credentialed programs, 15% in remedial programs, and less than 1% in work-based (on-the-job and

apprentice) training programs (Trade Act Participant Report).

For a subset of this data (2001 to 2007), I am able to observe the most targeted post-training

occupations and most frequent occupational transitions using USDOL-ascribed occupational codes

(O*Net 4.0 8-digit codes). Consistent with expanding industries during this period, the most targeted

occupations from TAA training were computer operators, ofﬁce clerks, transcribing-machine operators,

medical assistants, and nursing aids. In terms of occupation switching, some workers choose training

programs to deepen industry-speciﬁc human capital, while others appear to enroll in training to expand

general human capital. For example, two of the most commonly displaced occupations during this

period were commercial aircraft workers and men’s clothing workers. Many commercial aircraft workers

retrained in areas that seem like natural transitions—becoming tractor operators and air conditioning or

refrigeration mechanics. However, another popularly targeted occupation among this same group was

medical assistants. Men’s clothing workers on the other hand, frequently retrained to become sewing

machine operators—choosing almost exclusively to deepen knowledge in their incumbent industries.

Alternatively, if TAA certiﬁcation is viewed as negative publicity, certiﬁed plants may lay off fewer higher-skilled workers

post-certiﬁcation, resulting in downward bias from the control plants’ composition of higher-skilled separating workers.

While ﬁrms can be reimbursed directly for providing on-the-job training to laid-off workers, this comprises a very small

share of overall TAA training activities.

3 Data Sources and Matching

This project uses two main administrative datasets, merging the history of TAA petitions to U.S. Census

Bureau administrative data.

3.1 TAA Historical Petition Database

I have ﬁrst acquired the universe of approved and denied TAA petitions (1974-2016) through Freedom

of Information Act (FOIA) requests at the USDOL. This dataset contains an observation for each petition

(roughly 84,000 in total),

and provides three critical pieces of information.

1. First, each petition contains the plant (establishment) name and address, which I leverage for

matching to Census Bureau establishments and the workers employed at those establishments.

2. Each petition contains a series of dates, including the petition ﬁling date, determination (TAA

approval decision) date, impact date, and eligibility expiry date (see Section 2 for deﬁnitions).

These are used for identifying and pulling the set of workers laid off in the eligibility window.

3. Crucially for the paper’s main identiﬁcation strategy, each petition also contains the last name of

the investigator assigned to each case. These names were intensively cleaned in close consult with

DOL ofﬁcials and validated with historical employee records.

The petition database additionally includes information on petitioner ﬁler types (company, union,

worker-group, or state career center), USDOL-assigned 4-digit Standard Industrial Classiﬁcation (SIC)

codes, the company’s main product or service (recorded as a qualitative value), and an indicator for

whether the petition was designated as part of the NAFTA-TAA program, TAA, or both. Finally, each

petition contains an estimate of the number of workers covered—a 3-year estimate spanning the entire

eligibility window discussed above, that assumes that every laid off worker would take up the program.

Filers come from a variety of industries, from well-known automobile manufacturing plants in

Michigan, to displaced port workers in Seattle. Table 1 shows the location of the top TAA ﬁling zip codes

and the industries associated with those zip codes in each decade of the program’s existence. Moving

from 1975 to 2016, ﬁling has gradually moved from manufacturing industries in “Rust Belt” states to a

more disperse set, both geographically and in terms value-added activities.

This includes about 8,400 petitions for the NAFTA-TAA program described in Section 2.

This was needed to calculate precise investigator leniency values. For example, this included tasks such as identifying

whether “Green” and “Greene” were the same or separate investigators.

3.2 Construction of LEHD Worker-Level Panel

I merge TAA petition data to the US Census Bureau’s Longitudinal Employer-Household Dynamics

(LEHD) administrative ﬁles. The LEHD ﬁles allow for the construction of a detailed person-level panel

dataset which tracks quarterly worker earnings, labor force participation (employment), and educational

status across employers, geographies, and time. The core data are compiled from employer-reported

Unemployment Insurance (UI) ﬁlings at the state-level for every paid employee (ES-202 forms). While

the LEHD data partnership spans all 50 US states and covers over 90% of US workers,

states approve

researcher requested data on a state-by-state basis. For this project, 24 states and the District of Columbia

approved data access.

I use the 2011 LEHD snapshot which provides a relatively balanced panel from

1990 to 2011 (see Appendix A.1 for further details). Leveraging each worker’s (de-identiﬁed) social

security number, I merge in worker age, gender, and race, from the Social Security Administration

Numident ﬁle (available in the LEHD Individual Characteristics File). Educational attainment variables

are also available for Decennial Census and American Community Survey (ACS) respondents (roughly

1 in 6 workers), while education imputes based on Census Bureau multiple-imputation and probabilistic

record linking methods are used for non-respondent workers.

Education can take four ordinal values:

1=Some High School; 2=High School Degree; 3=Some College; 4=College Degree.

There are some important caveats imposed by the data limitations discussed above. Figure 3

compares the number of estimated TAA workers covered by ﬁled petitions in all states (cumulated

over the entire TAA history from 1974 to 2016), against the number of ﬁlers in the 24-state LEHD

sub-sample from 1990 to 2011. These are mapped to 1990 Commuting Zone (CZs) geographies, which

are the central unit of analysis when measuring the effects of TAA on spatial mobility.

The ﬁgure

reveals that while ﬁlers are generally concentrated in “Rust Belt” and southern manufacturing states,

the LEHD sub-sample is missing some notable political swing states such as Michigan, Wisconsin, and

Ohio (however contain others such as Pennsylvania).

Secondly, as is the case in most labor settings however, the LEHD cannot distinguish between a

number of cases that may be the cause of a missing earnings value. Following standard practice, I

designate a worker as unemployed if she has a missing earnings value between two positive earnings

observations. However I cannot discern between unemployed workers versus those who are retired,

As part of the non-included 10%, the LEHD excludes workers who are self-employed, agricultural workers, and some

government employees. See Abowd et al. (2009) and Vilhuber and McKinney (2014) for further details.

These include AR, AZ, CA, CO, DC, DE, FL, IA, ID, IL, IN, KS, MD, ME, MO, MT, NM, NV, OK, OR, PA, SC, TN, WA, WV.

All effects of TAA on formal education are robust to using both imputed and non-imputed measures. It also bears noting

that while worker occupations are available for ACS respondents, these data were not made available for the current draft

however will be explored in future work.

Using the deﬁnition from Dorn (2009), “Commuting Zones (CZs) provide a local labor market geography that covers the

entire land area of the United States. CZs are clusters of U.S. counties that are characterized by strong within-cluster and weak

between-cluster commuting ties.“

deceased, reliant on extended take-up of social insurance programs such as disability insurance,

self-employed, or discouraged from the labor force. Importantly, I also cannot know whether a worker

with a missing earnings value is in fact employed in a state outside of the set of 24 approved for this

project. This limitation would be most problematic for mobility estimates. In robustness tests, I thus

show that the main effects are stable when using the more contiguous West Coast states shown in Figure

3 which are less likely to feature mobility outside of the region.

3.3 Matching TAA Petitions to Displaced Workers at LEHD Employers

To be able to detect a potentially small effect size of TAA in noisy earnings data, I desire as conservative

a matching strategy as possible. To identify TAA ﬁlers at the worker-level, I ﬁrst have to identify both

the correct TAA petitioner plants and the timing of the separation event in the LEHD.

Beginning with identifying TAA plants, the 2011 LEHD snapshot contains each establishment’s State

Employer Identiﬁcation Number (SEIN) and federal Employer Identiﬁcation Number (EIN), however

does not directly report business name and address.

Using commingled IRS and Census data from the

Business Register—the Census Bureau’s most comprehensive database of U.S. business establishments

(formerly Standard Statistical Establishment List)—I am able to assign a company name and address to

each EIN in the LEHD, and subsequently match LEHD plants to TAA petitioners on cleaned company

names and addresses.

I keep only the ﬁrst TAA petition associated with any given plant so that no worker is assigned

to both the treatment and control group due to multiple ﬁlings. I then match TAA plant addresses to

Business Register addresses in both the calendar year of the petition and the year prior to the petition

(to account for any potential ﬁling lags or measurement error in ﬁling dates).

Finally, I keep matched

LEHD establishments if the plant address is unique to a given state-year cell. By focusing on one-to-one

matches, this circumvents problems arising from matching one TAA establishment address to a Census

location containing many establishments at the same address (such as an ofﬁce building). The sample

should thus be interpreted as representative of rural, stand-alone, manufacturing plants. I then repeat

this exact same procedure for company names, extensively cleaned in both datasets.

Drawing three random samples of 100 TAA petitions, I manually cross-check company names and

addresses and verify a match rate of 98%, with the residual likely owing to discrepancies between parent

and subsidiary names which could not be reconciled between the two datasets. This results in a ﬁnal

matched sample of 4,700 unique TAA establishments—comprising roughly 13% of plants associated

Each EIN and SEIN may have multiple and distinct units. For details on how this is dealt with, see Appendix A.1.

I build a comprehensive address cleaning ﬁle based on other papers, including code generously provided by Monarch et

al. (2017) who also match TAA plants to Business Register addresses.

with TAA claimants from 1990 to 2011. Finally, each matched plant’s SEIN number can then be used

to pull all workers employed at those plants during the eligibility window described in Section 2.2.

The ﬁnal step is to pull the full job history for each of these workers, and identify which workers

separated or were “displaced”—deﬁned here as moving from positive non-positive earnings during

the TAA eligibility window.

For further details on this procedure, please see Appendix A.1.

3.4 Sample Restrictions and Summary Statistics

Having identiﬁed TAA-eligible displaced workers associated with both approved and denied petitions,

I implement a number of sample restrictions to focus on those who are most likely to take up training

were they randomly assigned TAA approval. As noted in Section 2.2, I keep workers only if they

were displaced in the year prior to the petition decision, which eliminates one third of the original

sample. I further restrict attention to working-age individuals (22-65) who make less than $50,000/year

(∼85th percentile) in all years prior to the petition ﬁling. This value is a commonly used threshold for

Department of Labor programs, and eliminates the spurious inclusion of CEOs, managers, and other

workers who are both unlikely to take up training and not the population of interest in this study.

Quarterly earnings are deﬂated to 2010 real dollars using a seasonally adjusted consumer price

index. For computational tractability, I further collapse worker earnings to the year relative to the

petition decision (event time τ). While workers can furnish returns from multiple employers, earnings

are aggregated such that each worker only has one earnings observation per relative year (the unit of

analysis). I include observations 10 years before and after the petition decision such that τ ∈ [−10, 10] .

These restrictions reduce the overall dataset from ∼25 million to ∼4.2 million observations and 287,000

workers (rounded as per Census Bureau disclosure requirements). Earnings and employment values are

left- and right-censored within each worker panel, however the main paper results are robust to both

censoring and replacing edge values with zeros.

Lastly, for comparability with the labor literature, I deﬁne a “High Labor Force Attachment”

sub-group as the preferred analysis sample of the paper. This includes workers with at least 8 quarters

of positive earnings in the pre-period at or above the full-time minimum wage equivalent ($7.25 * 2,082

average working hours in 2010 ≈ $15,000 annually).

This results in a ﬁnal sample of 177,000 displaced

workers. However, all main results are robust to using both the high attachment sub-sample and the

unrestricted sample.

Workers can furnish returns from multiple employers, but earnings are aggregated (collapsed) such that each worker only

has one earnings observation per quarter.

This window takes maximal advantage of the 21 years of data spanned by the LEHD.

Further restrictions on the petitioner side include keeping only those petitions assigned to investigators with more than

10 cases, to eliminate potential noise associated with investigator leniency rates calculated from small cells.

Table 2 shows summary statistics for both groups, pooled across all periods (pre-period balance

statistics are presented in the next table). Starting with panel A, workers in both samples are largely

middle-aged, predominantly white, and slightly skewed toward being female. Worker high school and

college graduation rates are almost exactly in line with national averages for the time period.

Because

they are included based on a separation event, worker earnings and quarters employed per year are

expectedly below national averages, with the average worker making $22,830 and $18,814 in each sample

respectively (see panel B). Workers have on average about 1 job, however there is large dispersion in the

worker’s total number of employers in a given year. As indicated by the county unemployment rate at

the time of ﬁling, these workers are in highly distressed local labor markets with unemployment rates

near 6.5% (BLS Local Area Unemployment Statistics).

I also report overall mobility rates expressed as the likelihood a worker remains at the ﬁrm,

industry, or commuting zone of the employer from which they initially separated. Regarding petitioner

characteristics (panel C), companies and worker-groups are the most common ﬁlers, followed by unions.

It bears noting that approval rates are much higher when companies ﬁle with respect to non-company

ﬁlers, which can be seen by comparing “TAA Approved” versus “TAA Denied” groups in either sample.

Both samples contain roughly 250 case investigators during this time period, who remain on average

for about 10 years with the Department of Labor and handle roughly 23 TAA cases over that tenure. To

see the extent to which approval rates map to standard measures of industry tradability and occupational

offshorability associated with those industries (presumably known to investigators), I merge in three

known indices from Mian and Suﬁ (2014), Autor and Dorn (2013), and Blinder (2007), which show that

higher tradability values are generally associated with the approved TAA groups. For details on their

construction at the industry-level, see Appendix A.2.

4 Empirical Framework

4.1 Limitations to Difference-in-Differences

The top panel of Figure 4 plots raw means for TAA approved and denied workers across their separation

events, relative to the year of the petition decision (τ = 0). At ﬁrst glance, one might look at this

ﬁgure and conclude that workers who are approved for TAA are observably no different than those that

are denied in the pre-period. The difference-in-differences (DID) common trends assumption appears

to hold visually, and thus we are tempted to interpret the post-period (lack of) differential earnings

response as a causal effect. However this is highly misleading for at least two reasons.

Ryan and Siebens (2012) show that post-1990 high school graduation rates were roughly 80%—consistent with adding the

three education values in the summary statistics—whereas college graduation rates were roughly 25%.

First, these means mask incredible heterogeneity in both levels and pre-trends. To see this, Appendix

B.1 expresses mean earnings differences between certiﬁed and denied TAA applicants by 2-digit SIC

codes (thin gray lines), overlaid with the aggregate difference from the top panel of Figure 4 (bold series).

Firstly, the ﬁgure shows a mild downward trend in overall earnings differences which likely reﬂects

wage declines in tradable production, and at the very least, warrants within-industry comparisons to

control for selection on tradability and its correlates. Even within industries however, we see both

positively and negatively selected pre-trends. In textiles for example, TAA approved workers exhibit

both differentially declining earnings and a lower level of overall earnings relative to non-TAA approved

workers, which might bias TAA effects downwards. Whereas in other support industries such as

aluminum manufacturing products and auto parts, TAA-approved pre-treatment earnings are much

higher than non-TAA earnings, which might bias TAA effects upwards. The overall point is there is

no good reason that approved workers should look like denied workers absent TAA. Secular trends for

workers at “tradable” goods plants confound post estimates.

Second and more subtle, even if the common pretrends assumption appeared to hold visually after

conditioning on covariates, TAA workers may respond differentially to the layoff event itself, relative to

non-TAA workers. Those working at non-tradable goods plants for example, may have a broader skill set

that would be more transferable after layoff to an automating plant. Or, plants producing tradable goods

may have higher union representation which may result in earnings looking similar pre-separation, but

may lead to differential preparedness for industry and occupational switching post-separation. In both

cases, one would need an even stronger visual test such as parallel post-trends absent the treatment, which

is not possible to test (even if these are necessary but not sufﬁcient conditions for identiﬁcation). Overall,

workers may be different for a number of reasons correlated with tradability, geography, demographics,

or heterogeneity in access to types of training, yielding DID estimates that are likely not credible.

4.2 Investigator Assignment and Leniency IV

TAA cases are assigned [to investigators] primarily based on investigator caseload, as well as previous

experience with a company or industry. Staff leave or other scheduling issues can be a factor as well.

—Correspondence with Ofﬁce of Trade Adjustment Assistance,

a (obtained via Department of Labor FOIA request, 12/15/2016)

To overcome the challenging selection problems involved in identifying the causal effects of TAA, I take

advantage of how petitions are assigned to case investigators. I deﬁne an investigator’s leniency as the

share of total cases approved over their entire tenure, less the current case (excluding those with less

than 10 cases over their tenure).

This “leave-one-out” leniency measure (also known as a“jackknife”

IV) thus varies by investigator and case, but is time-invariant.

According to the assignment mechanism described in the quote above, TAA assigns two otherwise

identical worker cohorts displaced from the same industry, different TAA approval probabilities

based on whether their case is directed to a more lenient versus strict investigator. I thus use this

leave-one-out measure of investigator leniency as an instrumental variable (IV) for assignment to TAA.

Yet as leniency may still be correlated with petitioner characteristics through industry specialization

and experience, I must also include a number of ﬂexible controls for each investigator’s industrial

concentration and experience. Conditional on the successful inclusion of these controls, I provide a

number of tests that show assignment based on caseload is effectively as if randomly assigned.

The intuition for how this instrument alters earnings results with respect to the naive DID estimator,

is shown in the bottom panel of Figure 4. Raw earnings are plotted for workers assigned to top and

bottom decile residualized leniency quartiles, obtained by ﬁrst regressing leave-one-out leniency on

4-digit SIC industry ﬁxed effects, quarter-of-ﬁling ﬁxed effects, and investigator industry concentration

and experience controls at the time of ﬁling (discussed in detail in the next section). Purging the IV of

these threats to randomization, the resulting plot is a conditional version of the “reduced form equation”

of a corresponding 2SLS procedure. Comparing means for workers assigned to very lenient (top decile)

versus very strict (bottom decile) investigator scores, we begin to see earnings patterns separate in the

post-period and ﬂatten in the pre-period. While these deciles reﬂect one moment of the data (preferred

estimates scale up the results by the inverse of the ﬁrst stage using the whole support of residualized

leniency), the plot illustrates the variation underlying the main results of the paper.

For a subset of years, the petition also lists the last name of the certifying ofﬁcer who assigned the case. For those cases, I

calculate leniency across investigator-certiﬁer cells, however all results are robust to using investigator cells alone, in addition

to investigator-certifying ofﬁcer cells.

Additional results show that investigator leniency is relatively stable within investigators over time. DOL investigators

do work on a number of cases beyond those associated with TAA, including for example Occupational Safety and Health

Administration (OSHA) cases. However these are not observed in the data and thus not included in the leniency measure.

While investigator leniency is the most, Belloni et al. (2012) propose a lasso method for selecting the most strongly

binding among a number of plausibly exogenous instruments. However in this paper, the only other investigator-level variable

available is an imputed investigator race variable based on last name, and I thus do not employ this method.

4.3 Estimation Strategy

I employ a two-stage least squares (2SLS) estimation strategy that tracks workers as they move across

employers using repeated (pooled) cross-sectional regressions over event time:

TAA

ijkt

= θLeniency

−p

j(i)

+ α

jkt

+ δ

jkt

+ λ

+ X

ijkt

+ ν

ijkt

(1)

ijktτ

= β

TAA

ijkt

+ α

jkt

+ δ

jkt

+ λ

| {z }

restoring randomness

ijkt

+ e

ijktτ

(2)

In the ﬁrst stage, worker i’s petition is assigned to investigator j in calendar year t. TAA

ijkt

is an indicator

variable equal to 1 if that worker is associated with an approved TAA petition.

Leniency

−p

j(i)

measures

the total share of cases approved by investigator j less the worker’s own petition p.

k indexes the

4-digit SIC industry from which the worker was displaced, and τ ∈ [−10, 10] is the year relative to the

petition approval decision at τ = 0. Outcomes Y

ijktτ

include worker earnings, quarters employed, formal

education, and the probability workers move 2-digit NAICS industries and commuting zones.

I include three assignment variables to control ﬂexibly for differential approval propensities among

highly specialized or experienced investigators. N

jkt

is the raw number of cases that an investigator j

has adjudicated in industry k by calendar year t. C

jkt

∑

jkt

is the concentration of industry k cases

assigned to investigator j by time t. While these may be correlated, they are not perfectly collinear due

to the fact that investigators are not balanced across the entire panel. To the extent that any remaining

unobserved ﬁxed factors at the industry level affect both investigator assignment and underlying worker

characteristics (e.g. geography, mean tradability), ﬁxed effects λ

are included, and further ensure that

the impact of TAA is identiﬁed from leniency comparisons within narrowly deﬁned industries. In

both stages, X

ijkt

are precision controls that are mostly time-invariant and measured in the baseline

(pre-application) period.

The coefﬁcients of interest are each β

, which are estimated in separate regressions for each τ. When

overlaid on an event-study style plot, these point estimates dynamically map out the effects of TAA over

time. Thee include placebo estimates for all τ < 0, which test for the effects of TAA prior to the worker’s

separation and petition for beneﬁts (i.e. periods in which we would not expect to ﬁnd any statistical

signiﬁcant differential effects of TAA).

I use the subscript j(i) to clarify that worker i is assigned to investigator j (j for “judge”).

This estimator is formally known as a “jackknife” IV (JIVE), whose ﬁnite sample properties have been explored in a

number of papers (Angrist et al. (1999), Ackerberg and Devereux (2011), Kolesar (2013)). What varies here, is that leniency is

calculated from the universe of petitions, similar to a split sample IV design (Angrist and Kreuger (1995)) with ﬁxed effects.

The exception to this is a polynomial in age and variables interacted with that polynomial, however these vary

mechanically over time and cannot be endogenously manipulated in response to the TAA treatment. Not shown in equations

(1) and (2) but indicated clearly in regression tables, calendar-year and ﬁler-quarter ﬁxed effects are included in most

speciﬁcations.

4.4 Randomization Tests and IV Assumptions

Like all instrumental variables, the leniency IV must satisfy three main conditions to recover a local

average treatment effect (LATE): excludability, relevance, and monotonicity (Imbens and Angrist, 1994).

Before turning to tests for these conditions however, it is useful to consider TAA approval as the latent

outcome of a selection model to understand why the quasi-experimental controls above are included.

Consider a simple model of TAA selection similar to the second stage in the above 2SLS procedure:

ijktτ

= β

{σ

+ Z

j(i)k

+ X

ijkt

> ξ

ijkt

} + e

ijktτ

(3)

Here, the approval indicator TAA

ijkt

is determined by whether the latent sum of three components

exceeds an unobservable worker-investigator admittance threshold ξ

ijkt

. First, leniency is assumed

separable into an investigator-industry shift (Z

j(i)k

) around an industry’s average tradability signal

(the industry approval rate shared by all investigators). Observable characteristics X

ijkt

for both

workers and investigators at the time of petition ﬁling further capture investigator experience terms.

A linear parametrization of this equation yields the 2SLS reduced form equation, where the inclusion

of λ

ﬁxed effects absorb both the independent effect of σ

, and demean (within-transform) the

investigator-industry speciﬁc leniency to yield an industry-invariant leniency measure.

ijktτ

= b

1τ

Leniency

−p

j(i)

+ λ

+ b

2τ

ijkt

+ e

ijktτ

(4)

For b

1τ

(the numerator of the 2SLS estimate) to be identiﬁed without the second term, λ

would need

to be uncorrelated with both the investigator’s leniency and industry-speciﬁc earnings. However we

have already seen that earnings levels vary dramatically by industry, and know institutionally that

highly concentrated investigators are assigned to speciﬁc industries. To the extent that this happens

in a transitory and not ﬁxed way, time-varying investigator concentration controls are also included in

ijkt

(though these turn out not to have much of an effect).

Excludability

While excludability cannot be tested directly, I present two strong pieces of evidence supporting

the claim that investigator leniency is orthogonal to pre-determined characteristics of petitioners

The choice of the level of aggregation of SIC ﬁxed effects and concentration controls depend on a trade-off between bias

and efﬁciency. The more narrow the industry grouping, the more likely differences in tradability and its correlates are controlled

for, but the less precise our estimates become due to sparser observations of approved and denied cases in each grouping. In

practice, I require a minimum of 10 approved and denied cases per investigator to be included in the regression. Robustness to

control choices are shown in Appendix C.2.

(conditional on concentration controls and ﬁxed effects), and that the instrument only affects worker

outcomes through assignment to TAA.

In Table 3, I test for random assignment of TAA petitions to DOL investigators by regressing the

instrument on pre-determined characteristics. If investigators were assigned to cases with particular

economic or demographic characteristics, we would expect to observe statistically signiﬁcant predictors

of higher leniency values. However, as we move through the columns from left to right, consistent

with randomization, very few covariates are predictive of the instrument. (When they are statistically

signiﬁcant, the coefﬁcients are economically so close to zero that they can be ignored.)

Starting with column (1), I report the baseline mean of all pre-determined characteristics prior to the

eligibility window (5 to 40 quarters before the petition decision inclusively). The dependent variable in

column (2) is the endogenous TAA approval indicator variable. Consequently, it is not surprising that

many of the coefﬁcients in this column are statistically signiﬁcant. Notably, in panel C, company ﬁlers

have approval rates that are on average 22 percentage points higher than the omitted ﬁler group (state

career centers), and TAA approved workers are more likely to be considered “tradable” according to the

Mian and Suﬁ (2014) deﬁnition.

The dependent variable in columns (3) to (5) is the investigator leniency IV. Columns (4) and (5)

add the three “randomness restoring” controls shown in the main speciﬁcation, where investigator

concentration controls include both C

jkt

and N

jkt

measures (deﬁned above). Adding these controls

only alter randomization results in minor ways—consistent with most variation being driven by

caseload-based assignment within industry, rather than time-varying industry assignment.

Since

the regressions presented here each include many covariates however, one may be concerned that the

oversaturation of the model with controls is what drives the zeros, rather than random assignment.

Column (6) thus shows p-values from separate regressions of the leniency IV on each covariate

independently. Here, as in all regressions, standard errors are clustered at the investigator level (the

level of randomization). Finally, all regressions contain quarter-of-ﬁling and calendar-year ﬁxed effects.

The second piece of evidence that assignment based on caseload is as if random, is that investigators

with low caseloads do not systematically differ in their leniencies from investigators with higher

caseloads. Figure 5 demonstrates non-parametrically, how neither investigator caseload nor tenure at the

Department of Labor are correlated with leniency. This rules out confounding stories such as cases being

assigned to more experienced investigators who regularly approve certain types of workers, or the idea

that lower caseload workers have different competencies which could be correlated with pre-determined

characteristics of the types of workers they approve—violating the exclusion restriction.

The movement from statistically signiﬁcant to insigniﬁcant baseline covariates is sharper when testing for balance within

any given relative year. This is shown in detail in Appendix C.2.

Relevance, First Stage, and Monotonicity

Figure 6 displays variation in the investigator leniency measure pooled across the program’s history, and

matched to the ﬁnal analysis sample. The top panel is obtained by ﬁrst regressing leniency on the three

quasi-experimental controls discussed above (added to the overall sample leniency for interpretation).

I then plot the number of petitions ﬁled across bins of this residualized leniency, which exhibits a

surprising degree of variation (kernal bandwidth and 5% tails withheld for conﬁdentiality). The plot

is then overlaid with a local linear regression of approval rates on residualized leniency to demonstrate

the ﬁrst stage with respect to the underlying variation. The bottom panel then compares this to a “raw”

(unresidualized) leniency measure in the data.

Table 4 reports companion ﬁrst stage estimates corresponding to equation (1) of the paper for the

“High Labor Force Attachment” sample. Column (1) includes the minimal set of controls needed for

identiﬁcation, while moving left to right adds precision controls and investigator characteristics (which

have already been shown to be uncorrelated with approval rates in Figure 5.) Baseline Controls include

means over 5 to 40 quarters prior to the TAA petition decision for the following variables: worker

earnings, quarters employed, worker tenure, and initial employer and state earnings. Full Regression

Controls reﬂect covariates estimated in the preferred speciﬁcation in subsequent tables, and include: race

and gender ﬁxed effects, a cubic in age fully interacted with baseline earnings and gender indicators,

ﬁler-state ﬁxed effects, ﬁler-type ﬁxed effects (company, union, worker-group), and a dummy variable

for whether a petition applied as part of the NAFTA-TAA program.

Interpreting the magnitude of the ﬁrst stage, a coefﬁcient of 0.60 can be interpreted as a 10 percentage

point increase in leniency (the share of cases approved) being associated with a 6 percentage point higher

approval rate. I report the F-statistic from an F-test on the excluded instrument, which is consistently

strong and robust despite conservative clustering. I report unadjusted F-statistics as leniencies are

measured from the entire history of investigators, and not estimated (consistent with the examiner

literature that does not adjust degrees of freedom). Finally, the data shown here use the main analysis

sample at the worker-level. When regressions corresponding to models (1) and (2) are estimated at the

petition-level using just petition data however, the ﬁrst stage coefﬁcient is closer to 1, a coefﬁcient which

is also routinely found in the examiner literature).

Overall, these results suggest that the instrument

indeed has a large amount of predictive power over worker approval for TAA.

Finally, I explore monotonicity. While the monotonicity assumption is difﬁcult to test explicitly, I

follow common practices in labor economics and conﬁrm that heterogeneous subgroups of the analysis

all contain a positive ﬁrst stage such that higher leniency scores weakly increase TAA probability,

There is also a large increase in the excluded IV ﬁrst stage F-statistics at the petitioner-level.

facilitating a local average treatment effect interpretation for compliers.

LATE Compliers

Before proceeding to the main results of the paper, it is worth highlighting which types of petitioners and

workers are expected to comply with the treatment. Borrowing from earlier notation, each TAA approval

decision can be thought of as a latent variable sum of an observable “tradability” signal σ

and subjective

adjudication noise Z

j(i)k

for each investigator j (see Dobbie and Song (2015) for a similar set-up). This is

expressed in Appendix B.2. The left panel orders mean industry approval rates from lowest to highest by

3-digit NAICS codes, calculated over all TAA cases from 1974 to 2016. These are highly correlated with

known measures of tradability. The right panel shows within-industry investigator variation around

the same mean approval rates, where the median is indicated with a black dot and range plot whiskers

reﬂect the 35th to 65th leniency percentiles within each industry.

The high-variance industries along the middle bracket of the support reﬂect the “marginal” cases

that are hard to adjudicate, and for whom the randomly assigned investigator is most likely to be

inﬂuential. Roughly 80% of workers are assigned to investigators with leniency rates between 0.2 and

0.8, which suggests that indeed most TAA applicants are not part of industries that are easily assessable

as having been impacted by offshoring or import competition. This raises an important concern about

the extent to which the results remain relevant to trade-shocked workers. If indeed industry tradability

is hard to adjudicate, the local average treatment effect may in fact represent the effects of training on a

different population rather than workers most adversely affected by trade. For example, if trade shocks

are correlated with technological upgrading or automation, the LATE will reﬂect some combination of

these. In additional results, I parse estimates by different regions of this support and ﬁnd no signiﬁcant

differences across low and high values of tradability.

Lastly, it is important to note that the LATE estimated here is in fact an intent-to-treat estimator which

mechanically understates the treatment-on-treated or “true” LATE. Without detailed take-up data at the

individual or plant-level however, one cannot conduct the desired bounding or decomposition exercises

that would help place these effects in a more general context, nor use intent to instrument for take-up as

is common with one-sided compliance models.

5 Main Results

5.1 Impact of TAA on Worker Earnings, Employment, and Formal Education

Table 5 reports the main effects of TAA on worker earnings using the regression speciﬁed in equation (2),

where event time τ is pooled across two periods (such that each row represents a separate regression):

Pre-Training: τ ∈ [−10, −1]; and Post-Training: τ ∈ [2, 10].

Starting with the post period, column (1)

shows baseline OLS estimates that are negative and statistically signiﬁcant, suggesting that TAA workers

receive on average $964 lower annual earnings after training. However, this estimate is not credible for

the myriad of reasons discussed above. When applying the leniency instrument in a 2SLS approach

in columns (2) through (6), the effect sign and magnitude dramatically change. Column (6) shows the

preferred TAA earnings estimate of the paper. Accordingly, TAA takers have on average $10,256 higher

annual earnings, relative to all-else-equal non-takers.

Successively adding precision controls from columns (2) to (6) only minorly alter effect sizes.

Particularly inﬂuential in reducing standard errors are controls added from columns (4) to (6). These

are potential signs that TAA effects may have important dimensions of heterogeneity by ﬁler type, local

labor market (including states), and demographics. Lastly, consistent with prior randomization results,

the pre-training period placebo estimates consistently show a precise zero. That is, there are assuringly

no differential earnings effects of TAA when we not expect there to be (prior to the worker’s separation).

Considering average baseline earnings prior to layoffs were $26,880 (Table 3), an effect size of

$10,256 implies a relatively large elasticity. To further understand these results, I reestimate equation

(2) separately for each period 10 years before and after the year of the TAA approval decision. The

results for these 21 regressions (using the preferred speciﬁcation from column (6) of Table 5) are plotted

in the top panel of Figure 7, where vertical lines partition the support into pre-TAA, during-TAA, and

post-TAA periods. The ﬁgure shows a clear and surprisingly pattern. Expectedly, workers inferred to

take up beneﬁts forego roughly $10,000 in income while training for two years. Perhaps unexpectedly

however, large initial returns decay over time. Annual incomes among TAA and non-TAA workers in

fact, fully converge after ten years. Further tests reveal that this pattern is not driven by differential

attrition.

As the vast majority of program participants enroll in two-year programs or less, I conservatively use this window (rather

than a 3-year training window) as the treatment period. For effects on earnings during training, see Figure 8 which shows more

granular annual effects over event time.

Variable deﬁnitions are analogous to those shown in Section 4.4. Baseline Controls include means over 5 to 40 quarters

prior to the TAA petition decision for the following variables: worker earnings, quarters employed, worker tenure, and initial

employer earnings. Full Regression Controls reﬂect covariates estimated in the preferred speciﬁcation in subsequent tables, and

include: race and gender ﬁxed effects, a cubic in age fully interacted with baseline earnings and gender indicators, ﬁler-state

ﬁxed effects, ﬁler-type ﬁxed effects (company, union, worker-group), and a dummy variable for whether a petition applied

as part of the NAFTA-TAA program. All speciﬁcations include the identiﬁcation controls needed for restoring randomness

according to equation (2), and standard errors are clustered at the investigator level (the level of randomization).

Importantly, the dependent variable here includes earnings values equal to zero when a worker is

unemployed, and is thus reﬂective of the joint earnings and labor force participation effect. To begin to

decompose these two mechanisms and rationalize the pattern of depreciation, the bottom panel of Figure

7 implements the same estimation but calculating the dependent variable as within-worker cumulative

earnings from τ = −10 to the event year on the x-axis on the left, and from τ = 0 on the right.

The results from these cumulative earnings regressions suggest that indeed, effects are being driven

by both earnings as well as labor force participation. The advantage to expressing earnings this way

instead of logging, is that one does not need to be concerned with logging earnings values of zero.

Appendix B.4 shows however, that logging produces very similar results. Furthermore, cumulative

earnings have an appealing interpretation. Ten years out, workers have approximately $50,000 higher

cumulative earnings relative to all-else equal workers that do not retrain. This pattern is fully stable to

using the larger “full” sample which does not only restrict attention to workers that were more highly

attached to the labor force (see Appendix B.3 for the corresponding ﬁgure, and Appendix C.1 for more

detailed event-year coefﬁcient estimates.)

Table 6 reports the main effects of TAA on number of quarters employed using the same speciﬁcation

and controls as before. Focusing on the preferred estimate in column (6), TAA-trained workers are

employed on average 0.64 more quarters each year in the post period (τ ∈ [2, 10]). The top panel

of Figure 8 shows the corresponding dynamic pattern of employment, which closely mirrors earnings

effects. Trained workers appear immediately more employable than non-trained workers, which further

suggests that there are no economically meaningful extra search costs after TAA workers exhaust

extended UI beneﬁts (a mechanism that we can thus tentatively rule out but return to when discussing

mobility effects). Back-of-the-envelope calculations suggest that roughly 67% of the prior earnings

pattern can be explained by this higher employment rate.

While the LEHD does not contain variables

for hours worked, I am able to test whether TAA affects the number of jobs a worker has in a given year.

If displaced workers that do not receive TAA beneﬁts face reduced hours in the labor market, this may

materialize as workers taking multiple part-time jobs. However, the bottom panel of Figure 8 conﬁrms

that there is no discernible effect on the number of jobs held.

If indeed training contributes a sizable beneﬁt that is capitalized into earnings, we may expect to

see differential take-up along formal education measures. Table 7 reports the main effects on two such

measures—the probability a worker has educational attainment greater than or equal to a high school

degree and “some college” respectively. As discussed before, a concerning caveat about this data is that

In cumulative earnings regressions, censored values are replaced with zeros.

Using denied worker annual earnings as a baseline ($23,468 from Table 2), I divide this by 4 to get quarterly earnings, and

multiply by 0.64 to attain the relative earnings return for each year in the post period (τ ∈ [2, 10]). I then calculate this as a

fraction of the cumulative earnings return just established: 33,793.92/50,0000 = .67

the measurement is both ordinal and sparsely populated. I show however in the table, that across all

speciﬁcations, there is no statistically signiﬁcant effect on the probability that a worker moves up the

formal education scale. This is robust to using the constrained sample for which education values are

not imputed, and the full sample included education imputes. Figure 9 demonstrates this clearly.

5.2 Heterogeneity and Mechanisms

The fact that TAA appears to increase earnings, that those earnings depreciate, and that there are no

effects on formal education (such as community college take-up), together suggest that TAA may only

augment short-run demanded human capital rather than the types of permanent capital that are known

to have more durable returns (Card (2001); Kane and Rouse (1995)). While there is suggestive evidence

that most effects are coming through training and not extended unemployment components of TAA,

there is also concern that trained workers are just getting bumped to the top of local labor market job

queues at the expense of other workers.

One way this might manifest itself is if trained workers stay in

the same industries and labor markets relative to untrained workers. Conversely, if TAA workers switch

industries and labor markets, this is more consistent with an adjustment friction story rather than labor

market crowd-out.

To begin to test these mechanisms, I expand the main regression speciﬁcation of the paper to account

for simple heterogeneity in pre-TAA characteristics such that regression coefﬁcients reﬂect within-group

causal effects. In the speciﬁcation below, I interact the main effects of TAA (mediated by investigator

leniency) with “High” and “Low” values of pre-treatment covariates in both stages.

TAA

ijkt

∗ 1(High)

= θ

Leniency

−p

j(i)

∗ 1(High)

+ θ

Leniency

−p

j(i)

∗ 1(Low)

+ ... + ν

ijkt

(5)

TAA

ijkt

∗ 1(Low)

= θ

Leniency

−p

j(i)

∗ 1(High)

+ θ

Leniency

−p

j(i)

∗ 1(Low)

+ ... + ν

ijkt

(6)

ijktτ

= β

1τ

TAA

ijkt

∗ 1(High)

+ β

2τ

TAA

ijkt

∗ 1(Low)

+ ... + e

ijktτ

(7)

The above speciﬁcation is analogous to equations (1) and (2), where equations (3) and (4) correspond

to the new ﬁrst stage. Ellipses (...) are shown to parsimoniously capture exogenous controls αC

jkt

δN

jkt

+ λ

+ X

ijkt

γ in all three equations. Unlike before however, I include 1(High)

and 1(Low)

as indicator variables for whether a worker is above or below the median of a certain pre-treatment

covariate, as well as interacted calender year and ﬁler-quarter ﬁxed effects so that estimates are

interpreted within subgroups. In this way, one can plot the main coefﬁcients of interest across two

simple heterogeneity groups (β

1τ

and β

2τ

) to test for heterogeneous treatment effects.

See Heckman, Stixrud, and Urzua (2006) for a nuanced view of how schooling and job signaling may play out in such

scenarios.

Training Quality and Duration

I begin by examining heterogeneity in training quality. While quality is unobservable, the Department

of Labor Trade Act Participant Report (TAPR) records average weeks trained for TAA participants on

a quarter-by-state basis, which varies based on ﬁscal resources committed to vocational training and

state education programs. Using duration data from 2001 to 2016, I deﬁne “High” and “Low” training

states with respect to the median weeks trained per person in each calendar quarter. Figure 10 shows

the overlaid results of the two coefﬁcients of interest, suppressing standard errors for clarity (however

statistical signiﬁcance is reported in Table 8).

Remarkably, workers that are located in high-duration states prior to their layoff (the series marked

with an “x”) do not exhibit the depreciating pattern that is common to those in lower training duration

states. While one might be concerned that in fact, lower training duration reﬂects drop-out rates or

other selected worker qualities, it is unlikely that an entire state features large enough selection effects

to explain this difference. In conjunction with previous evidence, I thus attribute the depreciation to

short-run demanded skills becoming obsolete (consistent with rapid skill-biased technological change

or an overall declining labor share).

Indeed, 62% of TAA training programs confer vocational degrees

with shorter program lengths than typical community college or 4-year college degrees. Whether these

vocational programs are responsive enough to more rapidly adapt to changing demand, or if instead

more human capital investment is needed to catch up to the frontier, requires more research. However

the results here provide some strong leads for future work in this area.

Effects on Spatial and Industrial Mobility

To analyze effects on worker mobility across commuting zones and industries, I ﬁrst rank counties by

the severity of their shock based on Bureau of Labor Statistics (BLS) unemployment rate data (Local

Area Unemployment Statistics), which I merge to the LEHD panel. I deﬁne high and low shock severity

regions based on whether the county in which a TAA-qualiﬁed worker was displaced was above or

below median unemployment in their quarter of separation.

Figure 11 reveals that workers displaced in slacker labor markets (higher unemployment counties)

have returns that are almost double those of low unemployment rate counties. Foregone earnings

are higher for workers in high-shock regions, which suggests they train for longer. However, the

vast majority of workers are located in high-shock counties, which is also evidenced by the summary

statistics. I thus interpret the main effects as being driven by high-shock regions, and subsequently

For a discussion of the potential determinants of the declining labor share in the United States, see Autor et al. (2017).

All results here are robust to using a level measure of local labor market distress, or a change over time.

examine high and low shocks separately when analyzing mobility effects.

Figure 12 shows the main mobility results of the paper. I ﬁnd that workers in highly disrupted

regions are more likely to switch both industries and commuting zones in response to training. Workers

are approximately 20 percentage points more likely to move commuting zones and 28 percentage points

more likely to switch industries (at the 2-digit North American Industrial Classiﬁcation System (NAICS)

level), with respect to the location and industry of their pre-layoff employer. These are large effects,

when compared with baseline mobility rates of 0.26 and 0.23 for commuting zones and 2-digit industries

respectively (subtracting baseline estimates in Table 3 from 1.)

While not as well identiﬁed due to potential selection concerns (but nonetheless supported by

common pre-trends), I also present suggestive evidence that positive earnings returns among “movers”

drive the overall effects relative to “stayers”. I deﬁne movers and stayers by their ex-post mobility

decisions, which may reﬂect a self-selected sample that differs along a number of unobservables. Figure

13 shows that the main earnings results of the paper map very closely to effects for movers.

Overall, while there is suggestive evidence that TAA-trained workers previously were bound by

adjustment frictions, the analyses above are not explicit tests for externalities. Whether TAA is effectively

expanding a feasible match radius or alleviating an informational friction remains prime ground for

future study.

If in fact these workers are facing trade shocks which are spatially correlated (and

industrially concentrated if sufﬁciently agglomerated in those regions), this might also explain why

earnings returns are especially strong among movers. These workers would need to have much larger

search radii to ﬁnd productive employment.

Whether these strong mobility responses reﬂect matching

or information frictions, liquidity constraints (Chetty, 2008), or both, also remains to be tested.

6 Cost Effectiveness

While the paper’s identiﬁcation strategy provides robust evidence of positive earnings returns and

higher mobility associated with TAA, this does not inform us about the social cost-effectiveness of the

program. Toward this second end, I compare the ten year stream of estimated TAA earnings returns as

beneﬁts, with average TAA expenditures on training, extended UI, and foregone earnings while training,

as costs.

I incorporate two important potential sources of deadweight loss (DWL): the excess burden

Results for low-shock regions are shown in Results for low-shock regions can be found in Appendix B.8.

By contrast, Figure B.6 shows the effects for stayers, which I interpret as those who by chance happen to get the remaining

jobs open in their local economies.

See Shimer (2007) for a framework analyzing the roles of search and skill mismatch frictions in unemployment.

In ongoing work, I am investigating this further by taking advantage of distances moved between employers.

For an alternative welfare analysis, Hendren (2016) proposes a “Marginal Value of Public Funds” approach which is

arguably more comparable across programs. I provide results using this approach in Appendix A.3.

from taxation (“leakage”from redistribution), and moral hazard search costs associated with extended

unemployment insurance transfers. These are incorporated as follows:

Beneﬁts =

Earnings Returns from TAA

z }| {

τ=10

∑

τ=2

(1 + r)

τ+1

(8)

Costs =

τ=1

∑

τ=0

Foregone Earnings + Training Costs (& DWL)

z }| {

−

+ (1 + e)Training +

UI Transfer Costs (Moral Hazard & DWL)

z }| {

( e + Ω) ∗ UI

(1 + r)

τ+1

(9)

Here, Beneﬁts are the discounted stream of relative TAA earnings returns for post-training years (τ =

2...10), with

parameter estimates taken from Appendix C.1.

Costs contain two main terms. The

ﬁrst term is the discounted sum of foregone earnings while training (

< 0 for τ ∈ [0, 1]) and average

expenditures on training, where Training = $6, 181.96 is calculated from the data shown in Appendix

B.5. e represents the excess burden required by taxation to ﬁnance each dollar spent on training (Okun’s

“leaky bucket”).

The second term is simpler because UI transfers from one agent to another only

implicate social costs through excess burden (e ∈ [0, 1]) and search disincentives induced by the transfer

scheme (Ω ∈ [0, 1]).

To simplify the analysis, I set Ω = 0.345 (=0.6/1.6 following Schmieder and Von Wachter (2016)).

Setting UI = $13, 181.96, again taken from Appendix B.5, we then solve the internal rate of return r that

equates net present beneﬁts to costs for different values of e. Following Heckman et al. (2010), I show

both private and societal internal rates of return to TAA for a range of excess burden values (where

private returns to workers only include foregone earnings costs associated with training.)

Internal Rate of Return to TAA

Leakage Parameter (e) Private Return Social Return

0% 49.5% 17.0%

25% 49.5% 9.1%

50% 49.5% 4.0%

75% 49.5% 0%

100% 49.5% -3.0%

Note that τ + 1 is in the exponent of the discount term to be consistent with prior notation. τ = 0 should be thought of as

year one, such that the social planner is positioned at τ = −1 when calculating the IRR.

This ﬁrst term reﬂects the opportunity cost of training resources which could otherwise be allocated to other activities.

That is, instead of including as costs (1 + e + Ω) multiplied by each annual UI value, UI could easily be incorporated into

beneﬁts which cancels out the ”1”. We thus only need to concern ourselves with dead-weight loss and distortion parameters.

Note: Private returns assume workers do not bear any of the incidence of any Ricardian effects induced by the excess burden

of taxation, hence their stability across different deadweight loss parameter values.

I estimate an internal rate of return (IRR) on TAA of between 0.0% and 9.1% for deadweight loss

values ranging between 0.25 and 0.75. I interpret this as a lower bound for at least two reasons. First,

earnings returns are calculated from an intent-to-treat (ITT) estimator which likely understates beneﬁts

due to imperfect compliance with the treatment (i.e. partial take-up of TAA attenuates earnings estimates

toward zero). Second, TAA may induce worker substitution away from other costly social insurance

programs such as disability insurance (DI), which would further decrease program costs.

One important caveat to the above calculations however, is that positive earnings returns are

estimated from a local average treatment effect (LATE) that does not capture the fact that ﬁrms may

be incentivized to lay off additional workers after learning of their TAA eligibility status. Nevertheless,

back-of-the-envelope calculations show that these are unlikely to outweigh potentially much larger

downward pressures. Finally, it bears noting that like other public programs, the additional public

revenue from taxation of increased earnings returns for TAA takers is not sufﬁcient to cover program

costs.

7 Concluding Remarks

One of the most prominent challenges facing low-income workers in a modern, global labor market,

is how labor will adjust to a rapidly changing and increasingly automated economy. Trade-impacted

workers have received a large share of this attention, which became particularly visible as a policy issue

during the 2016 Presidential Election. While low-income households have beneﬁted tremendously from

trade in terms of lower costs of goods, higher variety, and quality of life improvements associated with

technological advancement, recent evidence suggests that they have also been persistently negatively

affected in terms of earnings and employment outcomes. Despite growing evidence that trade’s

disperse beneﬁts also come with concentrated costs, little is known about policy efforts that deliberately

target the adjustment process for those most affected by regionally and industrially shocked labor

markets. Credible empirical estimates are made difﬁcult by both a lack of detailed worker-level data

and confounding factors correlated with qualifying for adjustment programs—selection biases which

generally preclude reliable estimates.

This paper estimates the causal effects of Trade Adjustment Assistance (TAA)—the United States’

largest and longest standing public incentive program for retraining—on worker outcomes, by

leveraging quasi-random assignment of TAA cases to investigators of varying approval leniencies. Using

Autor et al. (2014) ﬁnd that DI is in fact the predominant margin through which workers adjust to trade shocks.

employer-employee matched Census data on 300,000 displaced workers, the paper provides evidence

of large initial returns to TAA. Workers inferred to take up beneﬁts forego roughly $10,000 in income

while training, yet ten years later have approximately $50,000 higher cumulative earnings relative to

all-else-equal workers that do not retrain. I estimate that 33% of these returns are driven by higher

wages—a sizable share which suggests that TAA-trained workers are not only compensated through

greater labor force participation or higher priority in job queues. Rather, TAA workers also appear to be

paid a premium for their newly acquired human capital. But these large relative gains also decay over

time, such that annual incomes among TAA and non-TAA workers fully converge after ten years. In

conjunction with two additional pieces of evidence—that TAA has no effect on formal education, and

diminishing returns are restricted to states with low training durations—I attribute this depreciation to

short-run demanded skills becoming obsolete (consistent with rapid skill-biased technological change

or an overall declining labor share). Indeed, 62% of TAA training programs confer vocational degrees

with shorter program lengths than typical community college or 4-year college degrees which have been

shown to have durable earnings returns.

In the most disrupted regions, workers are more likely to switch industries and move to labor

markets with better opportunities in response to TAA, suggesting a potentially important role for

human capital in overcoming adjustment frictions. However, one limitation to the study is that I do not

identify whether TAA is effectively expanding a feasible job match radius for its participants, or instead

alleviating other frictions, which may include worker present-bias, household liquidity constraints, and

other hypotheses. If in fact these workers are facing trade shocks which are spatially correlated (and

industrially concentrated if sufﬁciently agglomerated in those regions), this might also explain why

earnings returns are especially strong among movers.

Lastly, a cost-beneﬁt analysis produces a conservative internal rate of return (IRR) on TAA between

0.0% and 9.1%. Despite this being a relatively low IRR, policymakers may still consider the efﬁciency

costs associated with TAA investments a worthwhile trade-off as a redistributive policy toward this

sub-population. This would be especially true if there were either other externalities associated with

TAA training, or current social insurance programs were shown to be insufﬁcient for these workers.

One outstanding and related puzzle is if labor markets signal high private returns to human capital

investments such as TAA training, and this study conﬁrms those high returns, then why are take-up

rates so persistently low? Future work will need to explain this puzzle, and further examine whether

the results from this paper are relevant to other types of labor market pressures such as automation.

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Figure 1. Manufacturing Employment and Real Output

NOTES—This ﬁgure shows seasonally adjusted data from the Bureau of Labor Statistics (BLS), retrieved from

FRED, Federal Reserve Bank of St. Louis. The solid line plots monthly US workers employed in manufacturing

industries (BLS Current Employment Statistics, CES3000000001). The dashed line shows a quarterly index of

nonfarm business sector real output (BLS Labor productivity and Costs) where 2009q1=100. In a similar ﬁgure,

Pierce and Schott (2016) show the upward pattern in output persists for manufacturing sector value added, which

suggests falling labor intensity drives the decline rather than secular stagnation. Source: BLS (2017)

Figure 2. TAA Filer Time Series (USDOL Estimates)

NOTES—This ﬁgure shows the estimated number of workers eligible for TAA beneﬁts as covered by petitions at

the Department of Labor. Worker estimates are generated by case investigators processing plant-level information

(at times acquired using subpoena power), and cover the entire 3-year eligibility window shown in the timeline in

Section 2. Recession quarters are indicated in gray, and taken from NBER Business Cycle Dating Committee data.

The ﬁnal matched analysis sample studies petitions ﬁled between 1990 and 2011 for a subset of 23 approved states

(see text for further details). Source: USDOL (OTAA) petition database attained via FOIA request; NBER Business

Cycle Dating Committee

Figure 3. Workers Filing for TAA: All (Top) versus LEHD Sample (Bottom)

NOTES—These maps show the cumulative number of TAA ﬁlers by 1990 commuting zone (geographies taken

from Dorn (2009)). The top sample reﬂects the universe of TAA ﬁlers from 1974 to 2016. The bottom sample

displays all ﬁlers in 24 LEHD-approved states from 1990 to 2011, forming the basis of the matched analysis sample.

Both maps display cumulative numbers by quintile. See Appendix B.7 for a population-weighted version of the

same maps. Source: USDOL (OTAA) petition database attained via FOIA request

Figure 4. Displaced Worker Earnings, naive Difference-in-Differences (Top)

versus Leniency IV “Reduced Form” (Bottom)

NOTES—These plots show locally smoothed polynomial regressions of annual earnings before and after worker

separation. Unconditional (top) and residualized (bottom) means are estimated for the main analysis sample:

working-age individuals (22-65) with 2 years of positive earnings above the annual minimum wage equivalent

prior to ﬁling ($7.25 * 2,082 average working hours in 2010 ≈ $15,000), earning less than $50,000 annually in the

pre-period. Monetary variables are deﬂated to 2010 US dollars, seasonally adjusted, and winsorized at 1% to limit

outliers. Leniency quartiles (bottom panel) are calculated across 250 investigators. Source: LEHD; USDOL

Figure 5. Leniency IV versus Investigator Caseload and Tenure

NOTES—These plots show the relationship between the main leave-one-out investigator leniency measure and:

(1) investigator caseload measured by number of petitions (top); (2) investigator tenure in total years (bottom).

Leniency, caseload, and tenure, are ﬁrst regressed on year-of-ﬁling ﬁxed effects. Residuals from these regressions

are then averaged across 100 quantile bins and plotted across the support of the x-axis variable. Residualized

values are added to the overall mean leniency rate for ease of interpretation. Source: USDOL historical employee

records acquired via FOIA request

Figure 6. Variation in TAA Investigator Leniency

NOTES—This ﬁgure plots the number of petitions ﬁled across bins of residualized leave-one-out investigator

leniency (see text for details), from the ﬁnal matched LEHD sample (kernel bandwidth and 5% tails withheld

for conﬁdentiality). The top plot is overlaid with a local linear regression of approval rates on residualized

leniency, meant to demonstrate the ﬁrst stage. The bottom panel shows the difference between residuaized and

unresidualized leniency measures. Source: USDOL historical employee records acquired via FOIA request, LEHD

Figure 7. Dynamic Effects of TAA on Worker Earnings

NOTES—These plots show the main 2SLS coefﬁcient estimates of the effects of TAA on annual earnings (top) and

within-worker cumulative earnings (bottom), dynamically across event years relative to the TAA petition decision

(τ = 0). Each point estimate is from a separate cross-sectional regression by event year. Cumulative earnings

are summed from τ = −10 to the event year on the x-axis. Vertical lines partition the support into pre-TAA,

during-TAA, and post-TAA periods. Sample restrictions and variable deﬁnitions are identical to those described

in Table 5, column 6 (the paper’s preferred earnings speciﬁcation). Dotted lines represent 90% conﬁdence intervals

with standard errors clustered at the investigator level. Source: LEHD; USDOL

Figure 8. Dynamic Effects of TAA on Labor Force Participation

NOTES—These plots show the main 2SLS coefﬁcient estimates of the effects of TAA on quarters employed (top)

and number of jobs held (bottom), dynamically across event years relative to the TAA petition decision (τ = 0).

Each point estimate is from a separate cross-sectional regression by event year. Baseline quarters employed and

number of jobs held are 3.56 and 1.11 respectively (Table 3, column 1). Vertical lines partition the support into

pre-TAA, during-TAA, and post-TAA periods. Sample restrictions and variable deﬁnitions are identical to those

described in Table 6, column 6 (the paper’s preferred employment speciﬁcation). Dotted lines represent 90%

conﬁdence intervals with standard errors clustered at the investigator level. Source: LEHD; USDOL

Figure 9. Dynamic Effects of TAA on Formal Education

Prob(Education ≥ High School Degree)

Prob(Education ≥ Some College)

NOTES—These plots show the main 2SLS coefﬁcient estimates of the effects of TAA on formal education take-up

using both imputed and non-imputed decennial census measures which are merged to the Census LEHD (see text

for details), dynamically across all event years relative to the TAA petition decision (τ = 0). Each point estimate

is from a separate cross-sectional regression by event year. Education can take four ordinal values: 1=Some

High School; 2=High School Degree; 3=Some College; 4=College Degree. Vertical lines partition the pre-TAA,

during-TAA, and post-TAA periods. Sample restrictions and variable deﬁnitions are identical to those described in

Table 7, column 5 (the paper’s preferred education speciﬁcation). Dotted lines represent 90% conﬁdence intervals

with standard errors clustered at the investigator level. Source: LEHD; USDOL

Figure 10. Heterogeneous Earnings Effects of TAA by State Training Duration

NOTES—This ﬁgure overlays two series of 2SLS estimates, corresponding to each β

1τ

and β

2τ

of equation (5) of

the draft where coefﬁcients reﬂect high and low training duration lengths. Each point estimate is from a separate

regression by event year, showing the effects of TAA on worker earnings interacted with high and low training

duration in the state and quarter in which the worker was laid off (pre-period). “High” and “Low” are deﬁned

relative to median training duration, which is calculated for each quarter across states using TAA performance

data from 2001 to 2016 (training duration data are not available prior to 2001). Vertical lines partition the pre-TAA,

during-TAA, and post-TAA periods. Besides the sub-sample from data limitations, remaining sample restrictions

and variable deﬁnitions are identical to those described in Table 6, column 5. Standard errors are suppressed

for exposition (see online appendix for underlying data and standard errors). Source: LEHD; USDOL Trade Act

Participant Report (TAPR), 2001 to 2016

Figure 11. Heterogeneous Earnings Effects of TAA by Labor Market Strength

NOTES—This ﬁgure shows two series of 2SLS estimates, corresponding to each β

1τ

and β

2τ

of equation (5) of the

draft. Coefﬁcients reﬂect workers displaced in high (top) and low (bottom) initial unemployment rate regions.

Each point estimate is from a separate regression by event year, showing the effects of TAA on worker earnings

by high and low training duration in the state and year in which the worker was laid off. “High” and “Low”

are deﬁned relative to median training duration, which is calculated for each quarter across states using TAA

performance data from 2001 to 2016 (training duration data are not available prior to 2001). Vertical lines partition

the pre-TAA, during-TAA, and post-TAA periods. Besides the data constraint from limited performance data,

sample restrictions and variable deﬁnitions are identical to those described in Table 5, column 6. Dotted lines

represent 90% conﬁdence intervals with standard errors clustered at the investigator level. Source: LEHD; BLS

Local Area Unemployment Statistics (LAUS)

Figure 12. Effects of TAA on Worker Mobility by Initial Labor Market Strength

NOTES—This ﬁgure shows two series of 2SLS estimates, corresponding to each β

1τ

and of equation (5) of the draft

where the dependent variables are the probability that a worker is employed in the same commuting zone (top)

and 2-digit NAICS industry (bottom) as the region and industry from which they initially separated. Estimates

are broken out for high shock unemployment regions, where each point estimate is from a separate regression

by event year. Commuting zones are deﬁned by 1990 boundaries originally geocoded by Dorn (2009). Baseline

mobility rates are 0.26 and 0.23 for commuting zones and 2-digit industries respectively, taken by subtracting the

values found in Table 3, column 1 from 1. Vertical lines partition the pre-TAA, during-TAA, and post-TAA periods.

Sample restrictions and variable deﬁnitions are identical to those described in Table 6, column 6. Source: LEHD;

USDOL; BLS Local Area Unemployment Statistics (LAUS)

Figure 13. Earnings Effects of TAA for Labor Market and Industry “Movers”

NOTES—This ﬁgure shows 2SLS estimates of the effects of TAA for workers who move commuting zones (top)

or switch 2-digit NAICS industries (bottom) in the post-period, relative to the region and industry in which they

were initially employed. This ex-post deﬁnition of mobility is used as a subgroup in a speciﬁcation similar to

equation (5) of the draft, where only coefﬁcients on movers are plotted here (see Appendix B.6 for analogous

results for “stayers”). Movers comprise approximately 47% and 56% of the sample for commuting zones and

industries respectively. Each point estimate is from a separate regression by event year. Vertical lines partition the

pre-TAA, during-TAA, and post-TAA periods. Sample restrictions and variable deﬁnitions are identical to those

described in Table 5, column 6. Dotted lines represent 90% conﬁdence intervals with standard errors clustered at

the investigator level. Results for low-shock regions can be found in Appendix B.8. Source: LEHD; USDOL

Table 1. Location of Top 10 “Trade Displaced” TAA Zip Codes

Rank 1975-1985 1985-1995 1995-2005 2005-2016

1. Flint, MI Seattle, WA Los Angeles, CA Fremont, CA

2. Detroit, MI (a) Fort Worth, TX Seattle, WA Detroit, MI

3. Detroit, MI (b) Houston, TX (a) East Chicago, IN Nashville, TN

4. Detroit, MI (c) Linden, NJ Long Beach, CA St. Louis, MI

5. Detroit, MI (d) Flint, MI San Jose, CA Wichita, KS

6. Detroit, MI (e) Los Angeles, CA Scranton, PA Dayton, OH

7. Saginaw, MI Houston, TX (b) Washington, NC Warren, OH

8. Dayton, OH Milwaukee, WI New York, NY Wilmington, OH

9. Kokomo, IN Toledo, OH Dallas, TX Los Angeles, CA

10. Ann Arbor, MI Framingham, MA Seattle, WA Detroit, MI

Affected

Industries

(Mode)

Motor Vehicles,

Parts, Accessories

Oil & Gas Extract.,

Exploration,

Services

Electronics,

Aircraft, Textiles

Auto Parts, Plastics

Aircraft, Computers

Pharmaceuticals

NOTES—This table reports the locations of the top ten “trade-displaced” zip codes as calculated from Department

of Labor estimates of the total number of workers eligible for TAA, as associated with ﬁled TAA petitions at the

plant level. The reported industry reﬂects the qualitative description associated with the top three to ﬁve modal

industries in the same decade using standard industrial classiﬁcation (SIC) codes ascribed to petitions by case

investigators. Source: USDOL (OTAA) petition database attained via FOIA request

Table 2. Descriptive Statistics for TAA Approved and Denied Workers

High Labor Force Attachment High & Low Labor Force Attachment

TAA Approved TAA Denied All TAA Approved TAA Denied All

(1) (2) (3) (1) (2) (3)

A. Worker Demographics (LEHD)

Age (time of ﬁling) 43.91 (10.93) 43.08 (11.09) 43.65 (10.99) 42.7 (11.13) 41.76 (11.16) 42.41 (11.15)

Female 0.54 (0.50) 0.50 (0.50) 0.53 (0.50) 0.56 (0.50) 0.52 (0.50) 0.55 (0.50)

Black 0.11 (0.32) 0.13 (0.33) 0.12 (0.32) 0.13 (0.33) 0.15 (0.35) 0.13 (0.34)

White 0.80 (0.40) 0.79 (0.40) 0.80 (0.40) 0.79 (0.41) 0.78 (0.42) 0.78 (0.41)

High School Degree 0.39 (0.49) 0.37 (0.48) 0.39 (0.49) 0.38 (0.49) 0.37 (0.48) 0.37 (0.48)

Some College 0.29 (0.45) 0.31 (0.46) 0.30 (0.46) 0.29 (0.45) 0.31 (0.46) 0.29 (0.45)

College Degree and Above 0.11 (0.31) 0.14 (0.35) 0.12 (0.33) 0.12 (0.32) 0.14 (0.35) 0.13 (0.33)

B. Worker Economic Variables (LEHD)

Annual Earnings ($1,000) 22.554 (13.511) 23.468 (14.793) 22.83 (13.916) 18.628 (13.904) 19.232 (15.136) 18.814 (14.294)

Quarters Employed 3.21 (1.28) 3.14 (1.33) 3.19 (1.30) 2.93 (1.42) 2.87 (1.47) 2.92 (1.44)

Quarters Employed (full-time equivalence) 2.77 (1.54) 2.71 (1.57) 2.75 (1.55) 2.28 (1.67) 2.22 (1.70) 2.26 (1.68)

Employed 0.79 (0.40) 0.76 (0.43) 0.78 (0.41) 0.74 (0.44) 0.7 (0.46) 0.73 (0.45)

# of Jobs / Year 0.95 (0.75) 0.92 (0.78) 0.94 (0.76) 0.94 (0.08) 0.91 (0.85) 0.93 (0.84)

Tenure (years at separation) 4.90 (3.71) 3.87 (3.24) 4.58 (3.60) 14.76 (14.52) 11.5 (12.29) 13.74 (13.94)

Init. Employer Mean Earnings ($1,000) 23.197 (5.628) 23.216 (5.596) 23.204 (5.617) 20.822 (6.59) 21.100 (6.338) 20.910 (6.513)

County Unemployment Rate (time of ﬁling) 6.51 (2.28) 6.4 (1.85) 6.48 (2.16) 6.43 (2.20) 6.40 (1.78) 6.42 (2.08)

Prob(Employed at Petitioner Firm) 0.66 (0.47) 0.66 (0.47) 0.66 (0.47) 0.63 (0.48) 0.64 (0.48) 0.63 (0.48)

Prob(Employed at Petitioner 2-Digit NAICS) 0.7 (0.46) 0.71 (0.45) 0.70 (0.46) 0.68 (0.47) 0.69 (0.46) 0.68 (0.47)

Prob(Employed in Petitioner Commuting Zone) 0.69 (0.46) 0.72 (0.45) 0.70 (0.46) 0.67 (0.47) 0.72 (0.45) 0.69 (0.46)

C. Petitioner Characteristics (DOL)

Company Filer 0.40 (0.49) 0.10 (0.3) 0.31 (0.46) 0.40 (0.49) 0.11 (0.31) 0.31 (0.46)

Union Filer 0.14 (0.34) 0.19 (0.39) 0.15 (0.36) 0.13 (0.34) 0.17 (0.38) 0.14 (0.35)

Worker-Group Filer 0.37 (0.48) 0.63 (0.48) 0.45 (0.50) 0.37 (0.48) 0.65 (0.48) 0.46 (0.50)

Investigator Caseload (no. of petitions) 22.83 (18.25) 22.27 (16.21) 22.66 (17.64) 23.05 (18.68) 22.44 (16.35) 22.86 (17.99)

Investigator Tenure (decades) 0.979 (0.942) 1.02 (0.879) 0.991 (0.925) 1.02 (0.950) 0.995 (0.872) 1.01 (0.928)

Prob(Tradable) (Mian & Suﬁ, 2011) 0.64 (0.48) 0.51 (0.50) 0.60 (0.49) 0.58 (0.49) 0.43 (0.50) 0.53 (0.50)

Offshorability Z-Score (Blinder, 2007) 0.29 (0.84) 0.09 (1.23) 0.22 (0.98) 0.25 (0.87) 0.02 (1.28) 0.18 (1.02)

Offshorability Z-Score (Autor & Dorn, 2013) 0.23 (0.86) 0.27 (0.79) 0.24 (0.84) 0.16 (0.84) 0.22 (0.78) 0.17 (0.82)

Number of Petitioners ∼3,100 ∼1,300 ∼4,300 ∼3,300 ∼1,400 ∼4,700

Number of Displaced Workers ∼123,000 ∼54,000 ∼177,000 ∼198,000 ∼89,000 ∼287,000

Number of Observations ∼1,811,000 ∼810,000 ∼2,623,000 ∼2,883,000 ∼1,307,000 ∼4,192,000

NOTES—This table reports means and standard deviations for approved and denied TAA petitioners, pooled across all periods (pre, during, and post-TAA).

Both samples are restricted to working-age individuals (22-65) making less than $50,000 annually in the pre-period, and restricted to ﬁrst-time ﬁlers. The

“High Attachment” sample requires 2 years of positive earnings above the annual minimum wage equivalent prior to ﬁling ($7.25 * 2,082 average working

hours in 2010 ≈ $15,000). Monetary variables are deﬂated to 2010 US dollars, seasonally adjusted, and winsorized at the 1% level to limit the inﬂuence of

outliers. Both samples contain 250 unique case investigators (rounded for conﬁdentiality). See text for variable descriptions. Source: LEHD, USDOL

Table 3. Testing for Random Assignment of TAA Petitions to Investigators

Baseline TAA Approved Investigator Leniency F-Test [p-value]

(1) (2) (3) (4) (5) (6)

A. Pre-Determined Demographics (LEHD)

Age (time of ﬁling) 40.771 0.0007* (0.0004) -0.00007 (0.0001) -0.00002 (0.00004) -0.00002 (0.00004) [0.4437]

Female 0.5248 0.0281** (0.0118) 0.0015 (0.0019) -0.0005 (0.0009) -0.0006 (0.0009) [0.5166]

Black 0.1147 -0.0415* (0.0229) -0.0081** (0.0033) -0.0035 (0.0026) -0.0034 (0.0025) [0.3025]

White 0.7957 -0.0192 (0.0151) -0.0018 (0.0025) -0.0001 -0.0020 -0.0001 (0.0020) [0.2819]

High School Degree 0.3865 -0.0057 (0.0069) -0.0020 (0.0015) -0.0011 (0.0012) -0.0010 (0.0011) [0.8490]

Some College 0.2936 -0.0110 (0.0068) -0.00189 (0.0015) -0.0007 (0.0011) -0.0006 (0.0010) [0.3707]

College Degree 0.1173 -0.0224** (0.0089) -0.0014 (0.0021) -0.0013 (0.0011) -0.0012 (0.0011) [0.3110]

B. Pre-Determined Economic Variables (LEHD)

Annual Earnings ($1,000) 26.880 -0.0021*** (0.0006) -0.0002 (0.0001) -0.0001 (0.00007) -0.00007 (0.00007) [0.0917]

Quarters Employed 3.5566 -0.0060 (0.0048) 0.0011 (0.0012) 0.0007 (0.0008) 0.0006 (0.0008) [0.0627]

Quarters Employed (full-time equivalence) 3.2330 0.0154*** (0.0041) 0.0011 (0.0009) 0.0002 (0.0004) 0.0002 (0.0005) [0.0586]

Employed 0.9236 0.0420** (0.0189) -0.0040 (0.0027) -0.0025 (0.0025) -0.0021 (0.0025) [0.2100]

# of Jobs / Year 1.1120 -0.0007 (0.0008) 0.0002 (0.0002) 0.0002* (0.0001) 0.0002** (0.0001) [0.2325]

Tenure (years at separation) 5.0390 0.0012*** (0.0004) 0.0002** (0.0001) 0.0001** (0.0001) 0.0001** (0.0006) [0.0291]

Init. Employer Mean Earnings ($1,000) 23.159 0.0008 (0.0024) 0.0006 (0.0004) 0.0005 (0.0004) 0.0005 (0.0004) [0.1070]

County Unemployment Rate (time of ﬁling) 6.6054 0.0070 (0.0059) -0.0001 (0.0012) 0.0005 (0.0009) 0.0008 (0.0009) [0.0952]

Prob(Employed at Petitioner Firm) 0.7409 -0.0114 (0.0171) 0.0005 (0.0022) -0.0012 (0.0019) -0.0012 (0.0019) [0.0423]

Prob(Employed at Petitioner 2-Digit NAICS) 0.7760 0.0177 (0.0211) -0.0004 (0.0029) -0.0007 (0.002) -0.0008 (0.0020) [0.7783]

Prob(Employed in Petitioner Commuting Zone) 0.6853 -0.0245 (0.0253) 0.0026 (0.0046) 0.0067** (0.0031) 0.0066** (0.0031) [0.4896]

C. Pre-Determined Petitioner Characteristics (DOL)

Company Filer 0.3267 0.2190*** (0.0436) 0.0024 (0.0072) 0.0012 (0.0079) 0.0016 (0.0079) [0.5251]

Union Filer 0.1415 -0.0068 (0.0491) -0.0043 (0.0086) -0.0038 (0.0085) -0.0038 (0.0086) [0.8211]

Worker-Group Filer 0.4354 -0.0643 (0.0469) 0.0001 (0.0070) -0.0024 (0.0075) -0.00152 (0.0074) [0.8612]

Investigator Caseload (no. of petitions) 23.2509 0.00001 (0.0009) -0.0003* (0.0002) -0.00008 (0.0002) -0.00005 (0.0002) [0.3175]

Investigator Tenure (decades) 0.9419 0.00002 (0.00003) -0.00004** (0.00002) -0.00004** (0.00002) -0.00004** (0.00002) [0.0177]

Prob(Tradable) (Mian & Suﬁ, 2011) 0.6008 0.0687** (0.0270) 0.0009 (0.0048) – – – – [0.0952]

Offshorability Z-Score (Blinder, 2007) 0.3076 0.0032 (0.0176) -0.0058** (0.0025) – – – – [0.0967]

Offshorability Z-Score (Autor & Dorn, 2013) 0.2533 -0.0121 (0.0103) -0.0021 (0.0018) – – – – [0.1812]

Filer Industry FEs (4-digit SIC) – yes yes yes

Investigator Concentration Controls – yes yes

Joint F-Test [p-value] – [0.0000] [0.0409] [0.2033] [0.1801] [0.1801]

Number of Petitioners – ∼4,300 ∼4,300 ∼4,300 ∼4,300 ∼4,300

Number of Employers – ∼86,000 ∼86,000 ∼86,000 ∼86,000 ∼86,000

Number of Displaced Workers – ∼177,000 ∼177,000 ∼177,000 ∼177,000 ∼177,000

Number of Observations – ∼1,381,000 ∼1,381,000 ∼1,381,000 ∼1,381,000 ∼1,381,000

NOTES—This table tests for random assignment of TAA petitions to DOL investigators. Observations are pooled from eligible separating workers in the

“High Attachment” sample 40 to 5 quarters before their petition decision, and restricted to ﬁrst-time ﬁlers. The sample includes working-age individuals

(22-65) making under $50,000 annually in the pre-period, with 2 years above the annual minimum wage equivalent prior to ﬁling ($7.25 * 2,082 average

working hours in 2010 ≈ $15,000). Column (1) reports the baseline mean. The dependent variable in column (2) is an indicator for TAA approval.

The dependent variable in columns (3) to (5) is the investigator leniency IV. Column (6) shows p-values from separate regressions of the leniency IV on

each covariate. Monetary variables are deﬂated to 2010 US dollars, seasonally adjusted, and winsorized at 1% to limit outlier inﬂuence. All regressions

contain quarter-of-ﬁling and calendar-year ﬁxed effects. Standard errors are clustered at the investigator level. ***p<0.01, **p<0.05, *p<0.10. Source:

LEHD,USDOL

Table 4. TAA Approval and Investigator Leniency (First Stage)

1(TAA) 1(TAA) 1(TAA) 1(TAA) 1(TAA)

(1) (2) (3) (4) (5)

Leniency (Leave-One-Out) 0.646*** 0.613*** 0.639*** 0.615*** 0.592***

(0.11) (0.11) (0.12) (0.12) (0.11)

Investigator # of Cases in Industry (N

jkt

) 0.00274*** 0.00278*** 0.00270*** 0.00268*** 0.00296***

(0.00) (0.00) (0.00) (0.00) (0.00)

Investigator Concentration in Industry (C

jkt

) -0.524*** -0.499*** -0.508*** -0.481*** -0.411***

(0.11) (0.11) (0.12) (0.12) (0.11)

Investigator Caseload (No. of Petitions) -0.0001 -0.0002 -0.0003

(0.00) (0.00) (0.00)

Investigator Tenure (Decades) 0.000003 0.000003 0.000004*

(0.00) (0.00) (0.00)

Filer Industry FEs (4-Digit SIC) yes yes yes yes yes

Calendar-Year & Filer-Quarter FEs yes yes yes yes

Baseline Controls yes yes

Full Regression Controls yes

Number of Petitioners ∼4,300 ∼4,300 ∼4,300 ∼4,300 ∼4,300

Number of Displaced Workers ∼177,000 ∼177,000 ∼177,000 ∼177,000 ∼177,000

Number of Observations ∼2,623,000 ∼2,623,000 ∼2,623,000 2,623,000 ∼2,623,000

F-Statistic on Excluded IV 32.76 29.07 31.04 27.63 27.21

NOTES—This table reports ﬁrst stage estimates corresponding to equation (1) of the paper for the “High

Attachment” sample, which includes working-age individuals (22-65) making under $50,000 annually in the

pre-period, with 2 years above the annual minimum wage equivalent prior to ﬁling ($7.25 * 2,082 average

working hours in 2010 ≈ $15,000). Baseline Controls include means over 5 to 40 quarters prior to the TAA petition

decision for the following variables: worker earnings, quarters employed, worker tenure, and initial employer

and state earnings. Full Regression Controls reﬂect covariates estimated in the paper’s preferred speciﬁcation, and

include: race and gender ﬁxed effects, a cubic in age fully interacted with baseline earnings and gender indicators,

ﬁler-state ﬁxed effects, ﬁler-type ﬁxed effects (company, union, worker-group), and a dummy variable for whether

a petition applied as part of the NAFTA-TAA program (see text). Monetary variables are deﬂated to 2010 US

dollars, seasonally adjusted, and winsorized at the 1% level to limit the inﬂuence of outliers. Standard errors (in

parentheses) are clustered at the investigator level. ***p<0.01, **p<0.05, *p<0.10. Source: LEHD, USDOL.

Table 5. Pooled Effects of TAA on Annual Earnings ($)

OLS 2SLS

(1) (2) (3) (4) (5) (6)

A. Post-Training

1(TAA Approved) -963.8*** 14,474.4* 14,335.4* 14,812.3* 13,112.8** 10,255.9**

(250.2) (8211.1) (8449.8) (8383) (6432.3) (5086.7)

B. Pre-Training [Placebo]

1(TAA Approved) -150.9 405.4 313.1 169.2 266.9 333.8

(246.7) (480.1) (499.8) (514.2) (677.8) (660.1)

Identiﬁcation Controls:

Filer Industry FEs (4-digit SIC) yes yes yes yes yes yes

Investigator Concentration Controls yes yes yes yes yes yes

Precision Controls:

Calendar Year & Filer Quarter FEs yes yes yes yes yes yes

Baseline Controls yes yes yes yes

Filer Type & NAFTA-TAA FEs yes yes yes

Filer State FEs yes yes

Demographic Controls yes

Number of Petitioners ∼4,300 ∼4,300 ∼4,300 ∼4,300 ∼4,300 ∼4,300

Number of Workers ∼177,000 ∼177,000 ∼177,000 ∼177,000 ∼177,0000 ∼177,000

Number of Observations (All Periods) ∼2,623,000 ∼2,623,000 ∼2,623,000 ∼2,623,000 ∼2,623,000 ∼2,623,000

NOTES—This table reports the main effects of TAA on annual earnings, pooled in the “post” and “pre” periods

separately such that each column presents two regression coefﬁcients. Each speciﬁcation corresponds to equation

(2) of the paper for the “High Attachment” sample, which includes working-age individuals (22-65) making under

$50,000 annually in the pre-period, with 2 years above the annual minimum wage equivalent prior to ﬁling ($7.25

* 2,082 average working hours in 2010 ≈ $15,000). Baseline Controls include means over 5 to 40 quarters prior to

the TAA petition decision for the following variables: worker earnings, quarters employed, worker tenure, and

initial employer and state earnings. Demographic Controls include: race and gender ﬁxed effects, a cubic in age

fully interacted with baseline earnings and gender indicators. Filer-type ﬁxed effects indicate whether a petition

was ﬁled by a company, union, worker-group, or career center (omitted). NAFTA-TAA is a dummy variable for

whether a petition applied as part of the NAFTA-TAA program (see text). Monetary variables are deﬂated to 2010

US dollars, seasonally adjusted, and winsorized at the 1% level to limit the inﬂuence of outliers. Standard errors

(in parentheses) are clustered at the investigator level. ***p<0.01, **p<0.05, *p<0.10. Source: LEHD, USDOL

Table 6. Pooled Effects of TAA on Quarters Employed

OLS 2SLS

(1) (2) (3) (4) (5) (6)

A. Post-Training

1(TAA Approved) -0.0127 1.368* 1.209* 1.175* 0.795** 0.642**

(0.72) (0.72) (0.62) (0.61) (0.38) (0.32)

B. Pre-Training [Placebo]

1(TAA Approved) -0.00116 0.43 0.0193 0.0157 0.0466 0.0587

(0.01) (0.30) (0.05) (0.05) (0.08) (0.08)

Identiﬁcation Controls:

Filer Industry FEs (4-digit SIC) yes yes yes yes yes yes

Investigator Concentration Controls yes yes yes yes yes yes

Precision Controls:

Calendar Year & Filer Quarter FEs yes yes yes yes yes yes

Baseline Controls yes yes yes yes

Filer Type & NAFTA-TAA FEs yes yes yes

Filer State FEs yes yes

Demographic Controls yes

Number of Petitioners ∼4,300 ∼4,300 ∼4,300 ∼4,300 ∼4,300 ∼4,300

Number of Workers ∼177,000 ∼177,000 ∼177,000 ∼177,000 ∼177,0000 ∼177,000

Number of Observations (All Periods) ∼2,623,000 ∼2,623,000 ∼2,623,000 ∼2,623,000 ∼2,623,000 ∼2,623,000

NOTES—This table reports the main effects of TAA on quarters employed, pooled in the “post” and “pre” periods