The Life-Cycle Implications of Temporary Employment Contracts

The paper examines the consequences of a labor market in which employment protections apply differentially to temporary versus permanent contracts — the arrangement in many, primarily European, countries — by asking how changes to employment protection legislation affect GDP, employment and income, and it argues that the answer differs sizably for workers of different ages. The motivating observation is that temporary jobs disproportionately employ younger workers and act as the main route out of unemployment for many of them, so a policy that changes the balance between the tiers is not age-neutral. “Temporary” is used in the broad sense of the European surveys the paper draws on: any job whose end is set by objective rules such as a date or the completion of a task, rather than the narrower sense of agency work. The headline counterfactual is the elimination of the two-tiered system by removing employment protections from permanent jobs, with a second family of counterfactuals that instead changes how long a firm may keep a worker on temporary contracts.

Seven observations, drawn from the European Union Labour Force Survey for 2019 and the LISS (Longitudinal Internet studies for the Social Sciences) panel run by CentERdata at Tilburg University, which is a probability sample of Dutch households surveyed annually from 2008 to 2019 with around 6,000 respondents a year to the work-and-schooling questionnaire. They are: temporary contracts are more common among younger workers (and regain some prevalence past age 65); they are more common among the less educated; transitions into temporary contracts account for over half of all unemployment-to-employment transitions; employees in temporary contracts are less likely to remain employed a year later than those in permanent ones; among the employed, temporary-to-permanent transitions are much more common than the reverse; temporary workers earn approximately 6% less after controlling for observable worker and job characteristics; and those who remain in temporary contracts experience about 1.5% lower annual growth in real per-hour income on the same controls. The author notes that the Netherlands is fairly average among European countries in the prevalence of temporary contracts (16.43% of all jobs in 2019 by the Labour Force Survey, 15.67% in LISS), which is what makes it a reasonable calibration target rather than a special case.

A panel regression with year fixed effects on log real hourly income gives a coefficient on temporary employment of -0.0578 (standard error 0.0088, clustered at the individual level, 17,524 observations on 4,858 individuals), and a regression of annual real hourly income growth gives -0.0151 for those in a temporary job in both years (standard error 0.0074, 10,925 observations on 3,087 individuals). The sample is restricted to individuals aged 20 to 64 working at least 30 hours a week; income is deflated by the Dutch consumer price index and converted to an hourly basis using reported average weekly hours. The controls are extensive — postsecondary education, potential experience and its square, hours bands, supervisory role, four constructed skill levels, sector, sex and nationality, with the growth regression adding first-year log income and its square and indicators for moving into or out of permanent jobs, supervisory roles and skill levels. These are associations conditional on observables, and the author says so: the estimates are described throughout as what employment in a temporary arrangement “is associated with,” and she explicitly allows that unobserved heterogeneity in the kinds of jobs and firms that use temporary contracts may remain.

Two things: workers direct their search toward whichever job type is best for them, and human capital evolves endogenously. Earlier structural work in this area relied on random search plus exogenous restrictions to generate steady-state employment in both contract types, so workers had no job-type choice; here a worker of given age, human capital and education chooses a sub-market, defined as a set of vacancies offering the same job type and the same expected value, and so trades matching probability against surplus share. Selection into each tier therefore occurs by age, human capital and education, and the resulting distribution of workers across job types matches the data — which matters for policy analysis precisely because the fraction of workers searching for each type is itself likely to respond to a policy change. The model is quarterly, with 180 periods representing labor force participation from age 20 to 65, a unit mass entering into unemployment each period, endogenous separations when idiosyncratic match productivity falls below a cutoff, and bilaterally efficient contracts, so that the wage specification affects only wages and not separation or mobility decisions. Firms pay a firing cost to separate from a permanent worker and nothing to separate from a temporary one; temporary contracts also expire with probability kappa, at which point the match must either convert to a permanent contract or end costlessly.

Employed workers’ human capital rises by one grid step with probability pi_G, which may differ between permanent and temporary contracts; unemployed workers face two distinct downside risks. With probability eta an unemployed worker suffers an obsolescence shock and redraws human capital from the initial distribution truncated above at their current value, so the redraw can never be an improvement; otherwise human capital falls by one step with probability pi_U. This two-part structure is what lets the model reconcile a modest median wage loss after job loss with the very large losses suffered by some workers. Because the production function has diminishing returns to human capital, expected wage growth on the job declines with age even though expected human capital gains are linear in time.

Sixteen labor-market moments are matched jointly, drawn from the Dutch Labour Force Survey for 2019, the European Union Structure of Earnings Survey for 2018 and the LISS panel; the estimated human capital accumulation probabilities are about 0.214 in permanent contracts and 0.206 in temporary ones, and temporary contracts expire with quarterly probability 0.163. The accumulation rates target average life-cycle wage growth and the permanent-temporary wage growth difference across three broad age groups; the unemployment-side parameters target the median and 90th-percentile wage losses after job loss. Two honest qualifications follow. First, the difference between the two accumulation rates is small — under 0.01 — and if the policy functions were held fixed and the two rates equalized, the model would still generate roughly 90% of the reported wage-growth difference purely from selection, so most of that difference in the model is sorting rather than technology. Second, the model matches the wage-growth difference (-0.0132 on simulated data against -0.0151 in the data) but cannot match the wage penalty: on model-generated data the temporary-contract wage coefficient comes out positive, at +0.0054. The author offers two candidate explanations — that workers in the data may not fully internalize the discounted value of protection and faster growth, and that unobserved job and firm heterogeneity absent from the model may be at work — and argues the counterfactuals are nonetheless informative because they turn on the role of protections in promoting human capital growth, which the model does reproduce.

Both job creation and job destruction rise, destruction rises by more, and the unemployment rate goes up; average human capital falls, and GDP net of search and firing costs falls by 5.80% in the “no pi effect” case and 6.54% in the “full pi effect” case. In the first scenario the human capital accumulation rate in permanent jobs is left unchanged; in the second it falls to the temporary-contract rate, on the view that protections were generating all of the wage-growth difference not explained by selection. Across the two, the quarterly share of jobs ending in separation rises by 4.86 and 5.01 percentage points, the quarterly probability that an unemployed worker finds a job rises by 13.79 and 12.56 percentage points, the total unemployment rate rises by 6.29 and 6.74 percentage points, and average human capital falls by 9.17% and 10.37%. Average idiosyncratic match productivity actually rises, by about 5%, because firing costs had been keeping some low-productivity matches alive; net output falls anyway, because the losses in human capital and employment dominate. The mechanism is cumulative rather than static: removing firing costs raises job destruction directly, more frequent unemployment spells erode human capital, and lower human capital raises job destruction further as firms shed less productive workers.

Because earlier work excluded human capital accumulation, and the author demonstrates that this is the decisive omission by re-running the same counterfactual in a version of her own model where human capital is fixed for life. Blanchard and Landier (2002) and Cahuc and Postel-Vinay (2002), consistent with Hopenhayn and Rogerson (1993), argued that the job-creation effect would dominate so that eliminating employment protections would raise employment and output. Setting the accumulation and loss parameters to zero, so that workers draw a human capital value on entry and keep it, reproduces exactly that: the unemployment rate falls by 4.51 percentage points and net GDP rises by 9.59%. With the human capital process restored, the same policy raises unemployment by 6.29 points and lowers net GDP by 5.80%. The author also positions this as reconciling structural work with the empirical literature: work including García-Pérez et al. (2019) and Fauser (2020) found that greater availability of temporary contracts raised young cohorts’ employment rates but left those cohorts with more time unemployed and a cumulative wage loss over their careers — a pattern the model now reproduces.

Neither GDP nor consumption moves monotonically to the new steady state, and the welfare answer depends on an incentive effect the paper explicitly declines to model. Average idiosyncratic productivity jumps immediately as low-productivity matches are destroyed; net GDP drops at once, partially recovers as firms post more vacancies, then falls again as the slow erosion of human capital arrives. Total consumption — net GDP plus leisure consumption — jumps up on impact as destroyed matches are replaced by leisure, then declines; it ends higher in the new steady state under the “no pi effect” case but lower under the “full pi effect” case. Welfare is computed, following Menzio and Shi (2011), as aggregate consumption discounted along the entire transition path rather than by comparing steady states, which is legitimate here because agents are risk-neutral. If removing firing costs does not change accumulation incentives, the reform delivers a welfare gain of 1.05%; under the paper’s own parameterization of the “full pi effect” case the gain is smaller but still positive, 0.88%. Rather than enumerate the frictions that might depress investment incentives, the author inverts the question and asks how large such an effect would have to be to flip the sign: the probability of a human capital gain would need to fall by around 20%, from roughly 0.206 to 0.164, for the policy change to produce a welfare loss. This is the paper’s most carefully hedged result — output, employment and wage effects are called robust to the alternative assumptions, welfare is not.

Younger workers gain and older workers lose: average wages are higher after the reform until around age 45, and average consumption until around age 40, after which both fall below their levels in the protected steady state. New entrants are unaffected on impact, since they draw human capital from the same distribution; the deviation grows with age as cohorts accumulate more unemployment spells over a working life. The wage gain for the young comes from the search side — with firing costs gone, firms post more vacancies, so workers can endogenously search for higher-value contracts and still match — and it is eventually swamped by the accumulated human capital shortfall. At ages close to retirement the job-finding probability actually falls, because firms are unwilling to post vacancies for workers whose remaining career, and now whose human capital, is small. The author reads this age profile as consistent with the empirical finding of García-Pérez et al. (2019) that expanding jobs without firing costs raised young workers’ employment but was associated with lower earnings later in life.

Raising the rate at which temporary contracts expire — so more workers end up protected — raises average human capital and net GDP in the long run and lowers unemployment, even though average market tightness falls; lowering it does the reverse. The baseline expiration probability is 0.163 a quarter. Because average human capital rises when the expiration rate rises, unemployment falls even as the ratio of vacancies to searching workers declines. Lowering the rate reduces average human capital and so lowers output and average wages at the new steady state, while raising the average job-finding rate among the unemployed — the same trade-off as in the firing-cost experiment, which is why the author describes these results as consistent with the main counterfactual. This lever is of practical interest because countries differ widely in how long temporary employment may last: the Netherlands requires a permanent contract after three consecutive temporary contracts or three years with the same firm, France and Germany cap temporary employment at 18 months, Spain at three years and Italy at two.

The claim is conditional and mechanism-specific: if the two-tier system is eliminated by removing employment protections, the resulting lower average human capital prompts lower GDP and employment, and the impacts differ significantly by age. The author does not claim to have measured the effect of an actual reform; the results are steady-state and transition-path comparisons within a model calibrated to the Netherlands, and the welfare sign is left explicitly contingent on how protections affect skill-investment incentives, which is described as outside the scope of the paper. The model’s acknowledged failure to reproduce the observed temporary-contract wage penalty is on the record, as is the possibility of unobserved firm and job heterogeneity behind the empirical estimates. What the paper does establish firmly is a modeling point with a policy edge: evaluations of employment protection legislation that omit human capital accumulation can get the sign of the output and employment effects wrong.