The effect of trial periods in employment on firm hiring behavior

Trial periods were introduced as part of the government’s response to the Global Financial Crisis and consequent weak economic conditions in New Zealand. In the context of the slowing growth and rising unemployment seen in late 2008, the Minister of Labour described trial periods for small and medium firms as a way of lowering the risks employers face, creating jobs and getting struggling jobseekers into the labor market.

See the December 11, 2008 media release: https://www.national.org.nz/news/news/media-releases/detail/2008/12/11/90-day-trial-period-to-provide-job-opportunities.

Section 67A of the Employment Relations Act 2000, which was added in 2009, describes a trial provision in an employment agreement as follows:

A trial period must be specified in writing in the contract, which can be permanent or fixed term, and must be agreed by both parties and signed before the employee begins work. Importantly, trial periods may be used for employees who have not previously been employed by the firm only.

Trial period policy is expected to affect firm hiring only if firms believe that trial periods genuinely make dismissing an employee easier. Although data do not exist which could definitely show that trial periods decrease dismissal costs, this subsection describes the legal requirements for dismissal with and without a trial period, and argues that trial periods lower the bar for dismissal. The following subsection discusses firms’ beliefs about how trial periods affect dismissal costs.

In New Zealand, dismissing an employee who is not currently on a trial period can be slow, costly, and risky for the employer. This applies equally if the employee was hired before her firm was eligible to use trial periods, her employment contract does not include a trial period provision, or she is beyond the first 90 days of her employment.

For context, we note that employment protection in New Zealand is low relative to the OECD average, and that this was true even before trial period policy was introduced (OECD 2015).

A dismissal without a trial period must meet two standards of fairness. First, it must be substantively fair, meaning that there was a valid reason for dismissal. Reasons for dismissal can generally be grouped into serious misconduct that justifies summary dismissal and less serious misconduct. Serious misconduct might include behavior such as fighting, direct disobedience, or dishonesty, and less serious misconduct might include behavior such as absenteeism, unsatisfactory work performance, or using abusive language.

http://communitylaw.org.nz/community-law-manual/chapter-18-resolving-employment-problems/personal-grievances-chapter-18/

If a dismissed employee feels he was let go unfairly (“unjustifiably,” in the terminology of the Employment Relations Act 2000), he can raise a personal grievance against his former employer. If the parties are unable to resolve the grievance between them, the next step is mediation, followed by the Employment Relations Authority (ERA). If either party is unsatisfied with the ERA’s determination, it may make an appeal to the Employment Court.

http://www.findlaw.co.nz/articles/4296/unjustified-dismissal.aspx

The main purpose of the trial period provision is to remove a dismissed employee’s right to raise a personal grievance based on unjustified dismissal. This removes a great deal of the risk to the employer associated with dismissal of a new employee, and thus reduces the risk of hiring a person whose fit for the job is imperfectly known. If a new employee is under-performing or a bad fit, or if a new position within the firm turns out to be unnecessary, the employee can be let go without the risk of court battles and legal costs. Dismissal can also be substantially faster in a trial period, because the employee need not be given behavior or performance goals and the opportunity to improve and meet them before it can occur. However, trial periods do not give employers the right to “fire at will.” Good faith principles still apply; the employer must have a reason for dismissal; and processes stated in the employment contract must be adhered to.

At times, a firm may wish to dismiss an employee when external shocks lessen demand for its products. Legally, this is not a valid reason for dismissal. Trial periods increase the ease of dismissing employees in such circumstances, but only to the extent that the firm has recent hires still within their trial periods.

Even prior to the introduction of trial periods, firms could use “probationary periods” to test the match quality of new employees. Probationary periods are significantly weaker than trial periods, whereas trial periods in New Zealand are akin to what are called probationary periods in other countries. With a New Zealand probationary period, employers are not immune to personal grievances based on unjustified dismissal. The only increase in flexibility comes from the uncertain hope that employers will be held to lower standards in legal disputes if a dismissed employee was on a probationary period.

See https://employment.govt.nz/starting-employment/trial-and-probationary-periods/probation-periods/ for details. Note that there is no legal limit for the length of probationary periods, and they can be used for employees switching roles with the same employer.

We would expect trial period policy to have a measurable effect only if firms know about trial periods and use them. Survey evidence shows that firms generally know about trial periods and understand their basic nature. A year after trial periods were first introduced, 74% of surveyed employers knew that employees must consent to trial periods and 70% knew that employees retain protection against discrimination and harassment (DOL, 2010); knowledge about trial periods is likely to be even higher among the 59% of firms that report using them (MBIE, 2014). Despite trial periods not being a “get out of jail free” card for employers, survey and interview evidence shows that employers view trial period policy as substantially reducing the cost and risk of dismissal, and therefore of taking on a new employee (DOL, 2010; DOL, 2012; MBIE, 2014). For example, in one survey 79% of employers reported using trial periods to check an employee’s suitability for the job before making a commitment (DOL, 2010), which suggests that they believe that trial periods lower the costs of dismissal.

Further supporting the argument that firms’ perceived dismissal costs are lower when using trial periods, Table 1 presents the distribution of contract type for new hires in 2012, using nationally representative survey data. It shows that 37.7% of new hires are permanent roles with a trial period, 41.7% are permanent roles without a trial period, and 20.7% are temporary roles. This highlights the prevalence of trial periods, and hence their value to firms.

Thus there is a reason to believe that trial period policy could have changed hiring behavior on a large scale.

Surveys report less about employees’ views on trial periods. Qualitative interviews show employees lacked in-depth knowledge of trial periods a year after they were brought in, though employees did understand the basic idea: trial periods are for employers to judge their suitability for the role and make dismissal much easier (DOL, 2010). An important lesson is that employees generally do not view trial periods as negotiable, but rather consider job offers to be conditional on accepting them, meaning that their only alternative is to walk away.

A concern for any DID analysis is whether other policy changes differentially affected the control and treatment groups. If this were the case, it would be difficult to isolate the causal effect of the one policy change we are interested in.

In the wake of the GFC, other policies were introduced especially to help small firms. The most important of these is the Taxation (Business Tax Measures) Act 2009, introduced to help smaller firms with the pressures of the recession by helping cash flows and reducing the time spent working through tax forms.

For more details, see http://www.ird.govt.nz/technical-tax/legislation/2009/2009-5/leg-2009-5-changes-to-help.html

Throughout 2009, the government fast-tracked US$500 million of publicly funded building projects with the aim of creating jobs and stimulating the economy.

For more details, see http://www.beehive.govt.nz/release/fast-tracked-public-projects-give-500m-boost

More broadly, economic difficulties in the wake of the GFC should have continuous effects across the threshold and thus should not bias our estimates.

This section presents a simple model of employer hiring behavior that motivates our empirical tests of the effect of the policy on quantity of hires.

3.1.2

With trial periods

Now consider the case after the government introduces trial period legislation. The firm has three options: it can offer the applicant a job without a trial period; offer the applicant a job with a trial period; or not offer a job. The applicant will always accept an offered job. An applicant hired without a trial period will work for the firm permanently. If the applicant is hired on a trial period, the firm observes p during t = 0, after which it faces the one-time choice of whether to retain the worker for period 1 onward or costlessly dismiss him. However, hiring the worker with a trial period imposes a cost c > 0 on the firm at t = 0.

A cost to using trial periods is necessary to rationalize some employees not being hired on trial periods even when they are available. Alternatively, this could be modeled as the applicant turning down the job offer with some positive probability if it is offered with a trial period. The cost could take many forms, such as increased administrative burden or decreased worker productivity through diminished morale or firm loyalty.

After learning the value of P, at the start of t = 1, the NPV of profits of retaining the worker is:

(2)NPVretain=∑t=1∞1(1+δ)t−1p=1+δδp$$NP{{V}^{retain}}=\sum\nolimits_{t=1}^{\infty }{\frac{1}{{{\left( 1+\delta \right)}^{t-1}}}p=\frac{1+\delta }{\delta }p}$$

Clearly, the firm will then retain the applicant if p > 0, will dismiss the worker if p < 0, and will be indifferent to retaining him if p = 0. For simplicity, we assume the distribution of productivity does not change following the introduction of trial period policy. Relaxing this assumption (e.g., if employees put in more effort when hired under a trial period) may alter the model’s predictions. We also abstract away from any substitution between trial periods and other types of contracts such as temporary contracts, and we conduct a detailed empirical analysis of temporary contracts described in Section 5.4.

Hence, we can use a normal distribution truncated below at zero to model the firm’s profits each period after the initial period if it hires the applicant on a trial period. Let ψ (p;μ,σ) denotes the cumulative distribution function (cdf) of p so that ψ (0;μ,σ) is the probability, from the firm’s perspective, that p is negative. Then the expected NPV of profits when hiring on a trial period is:

(3)E[NPVhire_trial]=E[p]−c+∑t=1∞1(1+δ)t([Ψ(0)]E[p|p]≤0]+(1−Ψ(0))E[p|p>0])=E[p]−c+∑t=1∞1(1+δ)t(0+(1−Ψ(0))E[p|p>0])=μ−c+(1−Ψ(0))∑t=1∞1(1+δ)t(μ+σϕ(−μσ)1−Φ(−μσ))=μ−c+(1−ψ(0))1+δδ(μ+σϕ(−μσ)1−Φ(−μσ))$$\begin{align}& E\left[ NP{{V}^{hire\_trial}} \right]=E\left[ p \right]-c+\sum\nolimits_{t=1}^{\infty }{\frac{1}{{{\left( 1+\delta \right)}^{t}}}\left( \left[ \Psi \left( 0 \right) \right]\left. E\left[ p\left| p \right. \right]\le 0 \right]+\left( 1-\Psi \left( 0 \right) \right)E\left[ p\left| p \right.>0 \right] \right)} \\ & \ \ \ \ \ \ \ \ \ \ \ \ \ \ \ \ \ \ \ \ \ \ \ =E\left[ p \right]-c+\sum\nolimits_{t=1}^{\infty }{\frac{1}{{{\left( 1+\delta \right)}^{t}}}\left( 0+\left( 1-\Psi \left( 0 \right) \right)E\left[ p\left| p>0 \right. \right] \right)} \\ & \ \ \ \ \ \ \ \ \ \ \ \ \ \ \ \ \ \ \ \ \ \ \,=\mu -c+\left( 1-\Psi \left( 0 \right) \right)\sum\nolimits_{t=1}^{\infty }{\frac{1}{{{\left( 1+\delta \right)}^{t}}}\left( \mu +\sigma \frac{\phi \left( \frac{-\mu }{\sigma } \right)}{1-\Phi \left( \frac{-\mu }{\sigma } \right)} \right)} \\ & \,\ \ \ \ \ \ \ \ \ \ \ \ \ \ \ \ \ \ \ \ \ =\mu -c+\left( 1-\psi \left( 0 \right) \right)\frac{1+\delta }{\delta }\left( \mu +\sigma \frac{\phi \left( \frac{-\mu }{\sigma } \right)}{1-\Phi \left( \frac{-\mu }{\sigma } \right)} \right) \\ \end{align}$$

where ϕ(⋅) is the probability density function (pdf) and Φ(⋅) is the cdf of the standard normal distribution.

See Greene (2002) for this formula of the expected value of a truncated normal distribution.

Figure 1 shows, for values δ = 0.1 and c = 0.5, how firm hiring behavior depends on the values of δ and σ, and how this changes when trial periods are introduced, based on the profit functions given in equations (1) and (3).

Figure 1

As stated earlier, without trial periods the firm will hire the worker if μ > 0 or to the right of the vertical line in the figure, regardless of the value of σ.

The value of hiring a worker without a trial period is not affected by the availability of trial periods, so when trial periods are available a firm will never hire a worker with μ < 0 without a trial period.

Consider a worker with μ > 0 in a world with trial periods. The firm will hire her with a trial period if the value of equation (3) is positive, and the line

(4)μ−c+(1−Ψ(0))1+δδ(μ+σϕ(−μσ)1−Φ(−μσ))=0$$\mu -c+\left( 1-\Psi \left( 0 \right) \right)\frac{1+\delta }{\delta }\left( \mu +\sigma \frac{\phi \left( \frac{-\mu }{\sigma } \right)}{1-\Phi \left( \frac{-\mu }{\sigma } \right)} \right)=0$$

shown as a dashed line in Figure 1 marks the boundary between not hiring (below) and hiring with a trial period (above).

Now consider a worker with μ > 0 who will always be hired (without a trial period) in a no-trial-period world. If trial periods are available, she will be hired with a trial period if the value of equation (3) is greater than the value of equation (1), i.e., if

(5)μ−c+(1−Ψ(0))1−δδ(μ+σϕ(−μσ)1−Φ(−μσ))>1+δδμ$$\mu -c+\left( 1-\Psi \left( 0 \right) \right)\frac{1-\delta }{\delta }\left( \mu +\sigma \frac{\phi \left( \frac{-\mu }{\sigma } \right)}{1-\Phi \left( \frac{-\mu }{\sigma } \right)} \right)>\frac{1+\delta }{\delta }\mu $$

and will be hired without a trial period otherwise. This boundary is shown by the solid diagonal line in Figure 1.

Overall, Figure 1 shows that the μ - σ plane is divided into four sections: workers with μ - σ combinations in section A will not be hired in either world; those in section B will be hired in the trial period world only and will be hired with a trial periods; those in section C will be hired in both worlds, with a trial period when it is available; and those in section D will be hired with no trial period in both worlds. Note that there are no μ - σ combinations that would cause the worker to be hired when trial periods are not available but not when they are available. Thus if any preferred candidates fall into section B of Figure 1, the model predicts that hiring will be higher when trial periods are available.

3.1.3

Heterogeneous effects

An important dimension on which firms differ is the prevalence of long-lasting new hires, and firms in certain industries tend to have more employee churn than others. To explore how expected employee tenure affects the impact of trial period policy, we augment the above model by assuming any worker in a job quits each period with some exogenous probability τ, after which the firm’s profits are zero. An increase in τ can be modeled as an increase in the firm’s discount rate, δ, and profits farther in the future are valued less because they are less likely to be realized.

Figure 2 replicates Figure 1, but it shows how the equations dividing firm behavior change when the discount rate increases to 0.4. Area B that represents hires caused by the policy shrinks with a higher discount rate. We thus predict that the effect of trial period policy will be larger in industries where employment relationships tend to last longer.

Figure 2

The model also trivially predicts that trial period legislation decreases the stability of employment, because an employee will be dismissed if his effect on firm profit is revealed to be negative.

This section extends the model from the previous section to show that, conditional on a hire being made, trial periods increase the probability a riskier applicant is hired.

Then the same risk-neutral firm considers whether to hire applicant a, applicant b, or neither with σa > σb Assume the distributions of μa, μb, σa, and σb are all independent and the support of the distribution of σ is unbounded above.

The independence of σ from μ is a strong assumption. It is sufficient but not necessary for the proof of proposition 3.2.3, and not required for the other propositions.

Proposition 3.2.1. If the riskier applicant, b, is hired when trial periods are unavailable, she is also hired when trial periods are available.

Proposition 3.2.2. For each combination of μ_a, μ_b, and σ_a, where μ_a > μ_b and μ_a > 0, meaning that candidate a is hired if trial periods are not available, there exists σ_b such that candidate b is hired when trial periods are available.

To illustrate, consider an applicant a with μ_a = 0.5 and σ_a = 0.5. Consider the values of μ_b and σ_b such that the firm hires a when trial periods are unavailable, and hires b when trial periods are available:

Figure 3 plots μ_b against σ_b. The area labeled B is the combinations satisfying equation (6).

Figure 3

Proposition 3.2.3. If neither applicant is hired when trial periods are unavailable, and one is hired when trial periods are available, then the higher variance applicant, b, is more likely to be the one hired.

These three propositions yield the prediction that, conditional on a hire being made, trial period legislation increases the probability that the riskier of two candidates under consideration will be hired.

This proposition does not require that the expected profitabilities of the two candidates are equal. Furthermore, the variance of profitability is conditional on the information the employer has about an applicant. An applicant may be riskier from the employer’s perspective because she has a shorter work history, or less work history relevant to a particular job. This motivates our examination of “risky” groups for whom employers have less information, such as young people, recent beneficiaries, and recent migrants.

We use data from Statistics New Zealand’s Integrated Data Infrastructure (IDI), the core of which is the Employer Monthly Schedule (EMS), a linked employer–employee data set derived from tax records that cover at a monthly level essentially every employment relationship in New Zealand. These data are linked to a variety of other administrative data at the individual and firm levels.

For most of our analysis, we restrict our sample to hires occurring in the period January 2005 to March 2014 which has comprehensive data and covers a substantial period before the first and after the second policy change. However, some of our specifications use a shorter sample period; in particular, those involving education leavers end in December 2012 because education data are required for the following year and, at the time of writing, were available only until December 2013.

Our key variables are obtained from the EMS table. We define a hire as a new employer– employee pair in the EMS that did not exist in the previous month. For most of our analysis, we restrict this and consider only new hires, defined as new employer–employee pairs that did not exist in the previous 5 years. This is to exclude those who appear to be hired by the same firm many times due to seasonal work, temporary work, or other such phenomena. New hires are also the more relevant measure because trial periods may only be used for employees who have never worked for the firm earlier, so any change in hiring behavior should be seen in this group.

The legal requirement is that the employee has never worked for the firm previously; since we have data on employment relationships from 2000 only, we consider an employee who has not worked for a firm in 5 years to have never worked for that firm.

We define firm size as the start-of-month head count of a firm, calculated by subtracting the number of hires (of any kind) from the total number of employees paid at any time in the month. The relevant firm size measure for trial-period eligibility is a head count of employees, whether permanent or temporary. Between the policy changes, an employee hired with a trial period by a firm with fewer than 20 employees could be dismissed within his first 90 days even if at that time the firm had grown to 20 or more employees. When other employees leave the firm or the firm hires multiple employees during the month, start-of-month size may not perfectly capture size at time of hiring. However, the number of firm months with eligibility affected by the difference between the two is likely to be low. To check that this minor mismeasurement does not affect our results, we also run specifications in which we exclude firms of size 19 or 20.

Note that our measure includes anyone paid by the firm as an employee, and so could in principle include working proprietors if they receive wages. We derive firm size this way to match the legal definition used for application of trial period law.

In calculating a firm’s number of hires, and in regressions at the hire level, we exclude people hired more than 100 times in the period January 2005–March 2014, assuming that these reflect data issues. The impact is small; for hires involving firms with 15–24 employees, 3,072 individuals and 9,360 new hires are dropped from a total of over 800,000 hires. These individuals are still subtracted off in deriving a firm’s start-of-month size.

We use additional information on people who are hired to investigate whether trial periods encourage the hiring of disadvantaged types or affect the duration of employment. Some detail can be gleaned from the EMS. We categorize a person as not having worked in the previous year if he received no wages in the data, and class him as having worked elsewhere the previous month if he was paid by a different employer.

Note we are able to observe employment in New Zealand only, so some non-workers may have in fact been working overseas previously. Any effects of such misclassification will be reduced to the extent that employers do not consider foreign experience to be a perfect substitute for New Zealand experience.

We also use the EMS to construct indicators related to duration of employment. We do not know specifically when within a month employees started or finished working for a firm, but we do know the number of consecutive months in which they were paid by the employer and use this as our measure of duration.

The EMS table does include fields that indicate the start and end dates of employment, but the quality of these variables is very poor and so we choose not to rely on them.

The EMS has certain limitations. In particular, we cannot tell the nature of the employment agreement (e.g., whether the contract is permanent, fixed term, or casual), whether the employee was hired with a trial period, whether a separation was voluntary or the employee was dismissed, the number of FTEs worked, or the occupation or role in which the employee worked. We thus supplement EMS data with data from the Survey of Working Life (SOWL), which was conducted in 2008 and 2012 and covered a representative

After applying survey weights.

We generate additional information about hires using the links between the EMS and other data sources. The IDI contains information on gender, age, and ethnicity.

The IDI contains ethnicity information from multiple sources, and individuals who have supplied their ethnicity multiple ways are more likely to state multiple ethnicities. To maximize consistency, we use ethnicity sourced from tertiary education where available, from school education where tertiary is unavailable, and from all other sources where neither of these are available.

The IDI also contains industry information for firms. Industry classifications come from Australian and New Zealand Standard Industrial Classification (ANZSIC) 2006 codes, and they are consistent for a firm over time. They divide firms into 19 divisions at the broadest level (level 1), and for much of our analysis we use more detailed level 3 ANZSIC 2006 codes that divide firms into 203 industries.

Two level 3 industries experienced large anomalous spikes in hiring in our data: central government administration (“O751”) in December 2009 and school education (“P802”) in February 2010. Central government administration employers are largely outside the focus of firm size range, but school education employers are included in our data in large numbers. The reasons for these hiring spikes are unclear, but we are confident that they do not reflect an employer response to trial period policy. To ensure that they do not drive our findings, throughout our regression specifications we include a dummy variable for firms or hires in each of these industry months, and our main results are also robust to us dropping these industries entirely.

To minimize time-varying unobservable differences between our treatment (small) firms and control (large) firms, for many specifications we limit our sample to firms with 15–24 employees.

Firm size is as at the start of the month in question. Thus a firm may be small 1 month, large another, and out of sample another.

Table 3 presents summary statistics for our data, separately for small firms (15–19 employees) and large firms (20–24 employees), and by period relative to the policy changes. The average number of firms employing each month is stable over time for both groups, though there are around 4,800 small firms in each month as opposed to around 2,700 large firms.

A large proportion of firms hire each month. From 54% to 68% of firms make any hires in a month, and from 42% to 56% of firms hire new employees each month. The difference between new hires and overall hires is likely to reflect phenomena such as seasonal workers who return to the same employer each year, and casual employees. Hiring rates are considerably lower in the between and post-periods for both small and large firms, reflecting the Global Financial Crisis.

Among firm months that hired new employees, large firms are slightly more likely to make more hires. The median number of hires is 1 for small firms each period, and falls from 2 pre-policy for large firms down to 1 in subsequent periods. The 75th percentile is 3 in all periods for large firms, compared with 2 for small firms.

The fourth section of Table 3 shows the percentage of new hires that are various types. Across firm sizes and periods, the majority of new hires results only in short-term employment; 43–47% of new employment relationships last 5 months or longer. The percentage is very similar in small and large firms both in the pre- and post-periods, and it is slightly higher in small firms than large firms between the policy changes. The percentage of new hires who were employed elsewhere the previous month is very similar in small and large firms pre-policy, at 51.4% and 51.6%, respectively, and it declines somewhat for both firm sizes in subsequent periods.

In the pre-period, workers of unknown quality of all types except those under 25 years old are equally common among small-firm and large-firm new hires. Around 17% of new hires are recent beneficiaries, 10% are recent jobseeker beneficiaries, 23% have not worked in the previous year, 16% are recent migrants, 10% are Māori or Pasifika under 25 years old, and 13% are education leavers. Among new hires at small firms in the pre-period, 43% are under 25 years old, whereas 41% at large firms are in this age range. The proportion of new hires of each disadvantaged type shifts with the GFC, and some types become more common and others less common.

Figure 4 shows the monthly behavior of the total number of new hires scaled by the total number of employees for various firm size ranges within our treatment and control groups.

Three-month moving averages are presented for ease of viewing.

Figure 4

The treatment and control groups are split into those very close to the 20-employee cutoff (18–19 employees and 20–21 employees) versus those further away (15–17 employees and 22–24 employees). The vertical lines show the introduction of the two policies. A policy impact would appear as a gap that opened up between the dotted versus solid lines after the first policy change, and closed again once trial-period eligibility was extended to all firms. The figure suggests parallel trends in hiring before the first policy change and presents no evidence of a policy effect on the number of new hires for small firms, and the lines of hiring behavior are not only parallel, but also virtually coincide in all periods. We examine the policy effect on the number of hires and test for parallel pre-trends more rigorously in Section 5.1.

This section investigates whether trial-period eligibility causes the average firm to increase the number of people it hires, as predicted by our model. We test the policy effect on the quantity of hiring by firms using the general formulation explained earlier, with the number of new hires by the firm in the month as the dependent variable. We estimate these specifications as negative binomial regressions to account for the count structure of the dependent variable.

We test and reject the null hypothesis that a Poisson regression is the appropriate specification for our data.

Our main specification is at the firm-month level and takes the form:

where j denotes firm and t denotes month.

The allocation of workers to plants within multi-plant firms in the IDI is unreliable, so our preferred specification is at the firm as opposed to plant level.

The coefficient α₂, on the interaction between × small, is our estimate of the policy effect. We expect α₁, which captures the pre-policy discrete difference between firms with 19 employees and those with 20 employees over and above the difference captured by the log firm size term, to be close to zero. Similarly, we expect α₃ to be close to zero because the sum α₁ + α₃ gives the discrete difference between firms above and below the cutoff after all firms can use trial periods.

5.1.1

Basic specification

The panels of Figure 5 show how the estimates of the coefficients of interest from regressions of number of hires vary as the firm sizes included change, based on the specification in equation (7). The full regression tables are shown in Table A1 in Appendix. We focus on new hires, meaning individuals who have not worked for the firm earlier, because employees who have previously worked for an employer cannot be rehired by that employer with a trial period.

Figure 5

Table 4

Policy effect for very small firms

Negative binomial regression
Dependent variable: Number of new hires
Between * size 1–4	-0.003
	(0.016)
Between * size 5–9	0.015
	(0.016)
Between * size 10–14	0.017
	(0.016)
Between * size 15–19	0.003
	(0.017)
Between * size 25–29	0.015
	(0.020)
Post * size 1–4	-0.013
	(0.014)
Post * size 5–9	-0.005
	(0.015)
Post * size 10–14	-0.014
	(0.015)
Post * size 15–19	-0.004
	(0.015)
Post * size 25–29	-0.028
	(0.018)
Observations	15,423,435
% of nonzero hires	15.9%

Notes: The table presents results from a negative binomial regression at the firm-month level of the number of hires, similar to Table A1 in Appendix, but expanding the firm size sample to 1–29 employees. The regression also includes firm size category fixed effects, month-in-year fixed effects, log firm size and level 1 industry fixed effects. Standard errors, in parentheses, are robust and clustered at the firm level.

Table 5

Heterogeneous policy effects, with various interaction variables

Dependent variable: No. of new hires	Proportion of jobs in lvl 2 industry	Proportion of jobs in lvl 2 industry with	Proportion of jobs in lvl 2 industry	Proportion of jobs in lvl 2 industry	Seasonality of lvl 2 industry (proportion of max to min hires in a season, March 2005– February 2009)	Firm growth in employment over
interaction variable	using a trial period (0–1)	no employer-funded training (0–1)	with a permanent contract (0–1)	lasting 5+ months, 2005–2008 (0–1)		previous 12 months (decimal)
Between * small firm	0.135	0.070	0.273	–0.008	–0.060*	–0.025*
* interaction variable
	(0.139)	(0.105)	(0.276)	(0.107)	(0.031)	(0.013)
Post * small firm * interaction	0.163	0.040	0.492*	0.078	–0.088***	0.000
variable
	(0.138)	(0.101)	(0.259)	(0.101)	(0.030)	(0.014)
Between * small firm	–0.021	–0.040	–0.238	0.011	0.097*	0.004
	(0.035)	(0.079)	(0.249)	(0.053)	(0.051)	(0.014)
Post * small firm	–0.036	–0.030	–0.443*	–0.038	0.131***	–0.003
	(0.034)	(0.074)	(0.235)	(0.051)	(0.048)	(0.014)
Between * interaction variable	–0.570***	–0.214**	–0.960***	–0.338***	0.077***	0.039***
	(0.113)	(0.086)	(0.238)	(0.094)	(0.026)	(0.010)
Post * interaction variable	0.038	0.091	0.151	0.002	–0.014	0.041***
	(0.115)	(0.083)	(0.231)	(0.089)	(0.025)	(0.012)
Small firm * interaction variable	–0.185**	–0.125*	–0.274	–0.051	0.053***	0.008
	(0.089)	(0.068)	(0.170)	(0.067)	(0.019)	(0.007)
Interaction variable	–15.960**	5.130**	–6.534**	–2.339**	0.567**	0.040***
	(7.516)	(2.351)	(3.114)	(1.124)	(0.273)	(0.006)
Small firm	0.028	0.077	0.233	0.011	–0.092***	–0.013
	(0.024)	(0.050)	(0.154)	(0.034)	(0.031)	(0.012)
Observations	817,449	826,206	826,206	835,338	834,972	716,514
Mean of interaction variable	0.234	0.729	0.913	0.513	1.444	0.129
Standard deviation of interaction	0.081	0.115	0.050	0.124	0.410	0.826
variable

Notes: This table replicates and presents key coefficients from our baseline regression from Table A1 in Appendix for firms sized 15–24, and also includes a different interaction variable in each column to look for heterogeneous effects of trial period policy. The sample period is from January 2005 to March 2014. The first column measures trial period use using the 2012 Survey of Working Life (SOWL) while the second and third columns use the 2008 SOWL only. The last four columns use administrative data to form the interaction variable. In constructing the seasonality of level 2 industries, we sum the total number of a season’s hires over March 2005-February 2009, and take the ratio of the season with most hires to the season with least hires. A firm has a “recent unfilled separation” if its size is less than it was in any of the previous 3 months. Firm growth in employment over the previous 12 months is calculated up to the last month’s firm size. Standard errors, in parentheses, are robust and clustered at the firm level.

The bold variable highlights the policy estimate of interest, in this table and in subsequent tables.

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

Table 6

Policy effect on the probability a new hire was a disadvantaged jobseeker

Dependent variable: Indicator for hire type	Beneficiary in past year	Jobseeker beneficiary in past year	Not worked in past year	Recent migrant	Under 25 years old	Maori or Pasifika under 25	Education leaver
Between * small firm	0.003	0.003	0.004	–0.003	–0.003	–0.000	–0.001
	(0.003)	(0.002)	(0.003)	(0.004)	(0.004)	(0.002)	(0.002)
Post * small firm	0.005	0.003	0.005*	–0.001	0.003	0.001	0.002
	(0.003)	(0.002)	(0.003)	(0.004)	(0.004)	(0.002)	(0.002)
Small firm	–0.001	–0.001	–0.003	–0.004	0.003	–0.002	0.000
	(0.002)	(0.002)	(0.003)	(0.003)	(0.003)	(0.002)	(0.002)
Firm size (ln)	–0.002	0.001	–0.002	0.009	0.004	–0.004	0.002
	(0.007)	(0.006)	(0.008)	(0.010)	(0.009)	(0.006)	(0.005)
Plant size (ln)	–0.002	0.000	0.004*	0.001	0.013***	0.009***	–0.004***
	(0.002)	(0.002)	(0.002)	(0.003)	(0.003)	(0.002)	(0.001)
Month-in-year fixed effects	Yes	Yes	Yes	Yes	Yes	Yes	Yes
Calendar month * 3-digit industry fixed effects	Yes	Yes	Yes	Yes	Yes	Yes	Yes
Observations	893,292	893,292	893,292	893,292	890,352	890,352	770,415
% hires of given type	18.2	11.4	24.9	18.2	41.6	9.7	12.1
R-Squared	0.030	0.031	0.035	0.092	0.122	0.027	0.010

Notes: This table presents the coefficients from linear probability regressions at the hire level where the dependent variable is an indicator for the hire being a particular type of disadvantaged jobseeker, as described in the column header. Recent migrants are those who had their visa stamped in the past 2 years. Hires are included only if the firms are of size 15–24 and the employee had not worked for the firm in the previous 5 years. The sample period is from January 2005 to March 2014 (December 2012 in the final column). Age is missing for a small proportion of individuals, which causes the lower observation count in columns 5 and 6. Small firms are those with fewer than 20 employees, which were eligible to use trial periods after the first policy change. Between and Post refer to the time periods relative to the two policy changes. A dummy for the plant having zero employment is also included. Standard errors, in parentheses, are robust and clustered at the firm level.

The bold variable highlights the policy estimate of interest, in this table and in subsequent tables.

***p < 0.01, *p< 0.10.

Table 7

Policy effect on the distribution of employment duration of new hires

Dependent variable: Indicator for employment lasting at least	2 months	2 months	5 months	12 months	24 months
Between * small firm	0.003	0.002	-0.002	-0.001	-0.002
	(0.002)	(0.002)	(0.003)	(0.002)	(0.002)
Post * small firm	0.007**	0.006**	0.000	-0.003	-0.001
	(0.003)	(0.003)	(0.004)	(0.003)	(0.003)
Small firm	-0.001	-0.003	-0.003	-0.001	-0.002
	(0.002)	(0.002)	(0.002)	(0.002)	(0.002)
Firm size (ln)	0.026***	0.014**	0.029***	0.025***	0.015***
	(0.006)	(0.006)	(0.008)	(0.007)	(0.005)
Plant size (ln)	-0.015***	-0.013***	-0.019***	-0.009***	-0.005***
	(0.001)	(0.001)	(0.002)	(0.001)	(0.001)
Age		0.013***	0.018***	0.015***	0.012***
		(0.000)	(0.000)	(0.000)	(0.000)
Age squared (per 100)		-0.015***	-0.020***	-0.016***	-0.012***
		(0.000)	(0.000)	(0.000)	(0.000)
Female		0.007***	0.006***	-0.006***	-0.011***
		(0.001)	(0.001)	(0.001)	(0.001)
On jobseeker benefit in previous year		-0.026***	-0.071***	-0.070***	-0.051***
		(0.002)	(0.002)	(0.002)	(0.001)
On sole parent benefit in previous year		-0.027***	-0.051***	-0.053***	-0.040***
		(0.003)	(0.003)	(0.003)	(0.002)
On supported living benefit in previous year		-0.056***	-0.090***	-0.082***	-0.056***
		(0.005)	(0.006)	(0.004)	(0.003)
On other benefit type in previous year		-0.031***	-0.055***	-0.055***	-0.035***
		(0.003)	(0.004)	(0.003)	(0.002)
Recent migrant		0.001	-0.033***	-0.040***	-0.032***
		(0.002)	(0.002)	(0.002)	(0.001)
No wage or salary income in previous year		0.017***	0.041***	0.045***	0.034***
		(0.001)	(0.002)	(0.001)	(0.001)
Worked at a different firm the previous month		0.015***	0.046***	0.055***	0.040***
		(0.001)	(0.001)	(0.001)	(0.001)
Maori		-0.012***	-0.028***	-0.027***	-0.020***
		(0.001)	(0.002)	(0.001)	(0.001)
Pasifika		-0.009***	-0.016***	-0.015***	-0.007***
		(0.002)	(0.002)	(0.002)	(0.002)
Asian		0.004*	0.007***	-0.002	-0.005***
		(0.002)	(0.002)	(0.002)	(0.002)
Other ethnicity		-0.006***	-0.012***	-0.010***	-0.008***
		(0.002)	(0.002)	(0.002)	(0.002)
Education leaver (in past year)		0.021***	0.027***	0.021***	0.009***
		(0.001)	(0.002)	(0.002)	(0.001)
Month-in-year fixed effects	Yes	Yes	Yes	Yes	Yes
Calendar month * lvl 3 industry fixed effects	Yes	Yes	Yes	Yes	Yes
Observations	723,084	671,073	671,073	671,073	671,073
% of hires of given type	76.8%	77.8%	48.3%	26.0%	14.2%
R-squared	0.118	0.125	0.146	0.123	0.099

Notes: This table presents the coefficients from linear probability regressions at the hire level where the dependent variable is an indicator for employment lasting at least a given length of time, as described in the column header. Hires are included only if the firm is of size 15–24 and the employee had not worked for the firm in the previous 5 years. The sample period is from January 2005 to April 2012. Small firms are those with fewer than 20 employees, which were eligible to use trial periods after the first policy change. Between and Post refer to the time periods relative to the two policy changes at the date of hire. A dummy for the plant having zero employment is also included. Standard errors, in parentheses, are robust and clustered at the individual level. The bold variable highlights the policy estimate of interest, in this table and in subsequent tables.

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

Table 8

Policy effect on long-term hires and employees moving between firms

Dependent variable	New hires who lasted 5+ months	New hires who were employed elsewhere previous month
Between * small firm	0.006	-0.002
	(0.015)	(0.017)
Post * small firm	0.006	-0.003
	(0.014)	(0.015)
Small firm	-0.013	-0.016
	(0.012)	(0.013)
Firm size (ln)	1.000***	0.948***
	(0.037)	(0.041)
Month-in-year fixed effects	Yes	Yes
Calendar month * lvl 3 industry fixed effects	Yes	Yes
Observations	835,362	835,362
% of nonzero hires of given type	30.1%	29.8%

Notes: This table presents the coefficients from negative binomial regressions at the firm-month level where the dependent variable is the firm’s number of hires as described in each column header. New hires are those who had not worked for the firm in the previous 5 years. The sample period is from January 2005 to March 2014, and firms included are those sized 15–24. Small firms are those with fewer than 20 employees, which were eligible to use trial periods after the first policy change. Between and Post refer to the time periods relative to the two policy changes. Standard errors, in parentheses, are robust and clustered at the firm level.

The bold variable highlights the policy estimate of interest, in this table and in subsequent tables.

***p < 0.01.

Table 9

Substitution between trial periods and temporary contracts

Dependent variable	On temporary contract, 2012	On temporary contract, 2012	On trial period, 2012	On trial period, 2012	On temporary contract, 2008	On temporary contract, 2008
Predicted probability of temporary contract from 2008 data, parsimonious	1.156***		–1.436***
	(0.220)		(0.223)
Predicted probability of temporary contract from 2008 data, full controls		1.364***		–1.230***
Predicted probability of trial period from 2012 data, parsimonious		(0.151)		(0.147)	–0.270**
Predicted probability of trial period from 2012 data, full controls					(0.135)	–0.521***
						(0.086)
Year	2012	2012	2012	2012	2008	2008
Observations	2,397	2,385	2,397	2,385	1,686	1,686
R-Squared	0.014	0.043	0.015	0.025	0.003	0.023
Mean of dependent variable	0.207	0.207	0.376	0.375	0.200	0.200

Notes: This table presents results from OLS regressions at the job level, exploring how being on different contract types correlates with the predicted probability of being hired on a certain contract type from a separate survey year. The dependent variable in each column is given in the column header. Predicted probabilities use the individual characteristics and job characteristics of each observation in the sample, and use the model of Table A8 in Appendix for the prediction. The sample is limited to those hired in the previous year. Standard errors, in parentheses, are robust.

***p < 0.01, **p< 0.05.

Table A1

Policy effect on the number of new hires, varying firm sizes included

Dependent variable		Number of new hires
Firm sizes included:	18–21	17–22	16–23	15–24	10–50
Between * small firm	0.008	0.009	0.009	0.008	0.012
	(0.019)	(0.017)	(0.015)	(0.014)	(0.009)
Post * small firm	-0.005	-0.002	0.003	0.000	0.010
	(0.017)	(0.015)	(0.014)	(0.013)	(0.010)
Small firm	-0.014	-0.000	-0.018	-0.014	-0.016*
	(0.016)	(0.013)	(0.012)	(0.011)	(0.009)
Observations	314,637	478,503	650,934	835,362	2,495,838
Firm sizes included:	17–18, 21–22	16–18, 21–23	15–18, 21–24	10–18, 21–50
Between * small firm	0.030	0.024	0.019	0.016*
	(0.020)	(0.017)	(0.015)	(0.010)
Post * small firm	0.010	0.012	0.006	0.013
	(0.018)	(0.016)	(0.015)	(0.010)
Small firm	0.032	-0.032	-0.020	-0.019*
	(0.028)	(0.019)	(0.016)	(0.010)
Observations	322,119	494,553	678,978	2,339,457
Firm sizes included:	16–17, 22–23	15–17, 22–24	10–17, 22–50
Between * small firm	0.009	0.006	0.014
	(0.020)	(0.017)	(0.010)
Post * small firm	0.008	0.001	0.013
	(0.019)	(0.017)	(0.010)
Small firm	-0.126***	-0.043*	-0.022*
	(0.039)	(0.025)	(0.012)
Observations	336,297	520,725	2,181,201

Notes: This table presents the coefficients from negative binomial regressions at the firm-month level where the dependent variable is the firm’s number of new hires. New hires are those who had not worked for the firm in the previous 5 years. All regressions also control for log firm size, month-in-year fixed effects, and calendar month * level 3 industry fixed effects. The sample period is from January 2005 to March 2014. Small firms are those with fewer than 20 employees at the start of the month, which were eligible to use trial periods after the first policy change. Between and Post refer to the time periods relative to the two policy changes. Standard errors, in parentheses, are robust and clustered at the firm level.

The bold variable highlights the policy estimate of interest, in this table and in subsequent tables.

***p < 0.01, *p < 0.10.

Panel A1 of Figure 5 plots the estimated policy effect and 95% confidence intervals from five different regressions, varying the firm sizes included in each regression. Our preferred specification is the 15–24 version, which balances power against homogeneity of treatment and control firms. The point estimate of the policy effect here is 0.008, implying that the policy caused a tiny and statistically insignificant 0.8% increase in the number of new hires by firms with 15–19 employees.

In a negative binomial regression, for a coefficient b, exp(b) gives the effect of a unit change in the independent variable on the dependent variable (rate of hires), so exp(b) = 2 would imply an increase of 1 corresponds to a doubling of the hiring rate.

The coefficient is sufficiently precisely estimated that we can confidently rule out an economically significant policy effect; the 95% confidence interval extends only to a 3.5% increase in hires. The point estimate remains close to zero when the firm size range is varied. Table A1 in Appendix shows that the coefficient on small firm also tends to be close to zero (between 0 and -0.016) and with small standard errors. This means, reassuringly, that our model finds no large discrete difference in hiring between our treatment and control firms in the pre-policy period after controlling smoothly for firm size.

Panel A2 of Figure 5 shows the corresponding placebo tests for the above regressions, plotting the coefficient estimates on post*small firm. As explained previously, the sum of the coefficients on small firm and post*small firm captures the discrete difference in hiring between firms on either side of 20 employees after the second policy change, which we expect to be close to zero. Reassuringly, these placebo coefficients are close to zero and precisely estimated across the ranges of included firm sizes.

To additionally test whether large and small firms were on parallel trends in the period before the policy was announced in December 2008, Table A2 in Appendix replicates our preferred specification from Figure 5 but limits the sample period from January 2005 to November 2008 and interacts a linear time trend with the small firm indicator. The coefficient on this interaction is precisely estimated as zero, showing that there was no meaningful preexisting difference in hiring trends between the treatment and control firms.

Table A2

Test for parallel trends in the pre-announcement period

Dependent variable	Number of new hires
Time trend * small firm	0.0002
	(0.0005)
Time trend	-0.0087
	(0.0054)
Small firm	-0.0143
	(0.0181)
Log of firm size	0.9632***
	(0.0448)
Calendar month * level 3 industry fixed effects	Yes
Observations	359,046

Notes: This table presents coefficients from negative binomial regressions at the firm-month level for firms with 15–24 employees, as in Table A2 in Appendix, but limits the sample period from January 2005 to November 2008, includes a linear time trend, and interacts the linear time trend with the small firm indicator. Standard errors, in parentheses, are robust and clustered at the firm level.

The bold variable highlights the policy estimate of interest, in this table and in subsequent tables.

***p < 0.01.

To minimize the effects of any misclassification of firms as treatment or control or endogenous selection of firms into the treatment group, Panels B and C of Figure 5 replicate Panel A, but exclude firms sized 19–20 and 18–21, respectively.

Full regression results are again shown in Table A1.

There is no marked change in the results; the estimated policy effect is slightly larger though still close to zero when excluding firms sized 19–20, and it is even smaller than in Panel A1 when excluding firms sized 18–21. In all cases, the estimated coefficients on post*small, the placebo policy effects, are close to zero. This suggests neither mismeasurement of firm size nor endogenous firm size is driving our results.

To further address endogenous selection, we replicated this analysis with the small firm variable defined by a firm’s size prior to the first policy change. Results, unreported, again suggest a policy effect close to zero, with small standard errors.

As an alternative to our negative binomial regressions, we run three OLS specifications with firms sized 15–24, presented in columns 5–7 of Table A3 in Appendix. The first is a linear probability regression where the dependent variable is an indicator for the firm making any new hires. The coefficients on between*small and post*small are both small and insignificant, providing no evidence of a policy effect. The second is an OLS regression where the dependent variable is the log of new hires plus one. Here the coefficient on between*small of 0.019 is positive and statistically significant, suggesting an economically small 1.9% increase in hiring. However, it is similar to the coefficient on post*small of 0.013, which means that it is probably driven by small differential changes in unobservable characteristics of the treatment and controls firms, and it is unlikely to indicate a genuine policy effect.

Our results are also not affected by our treatment of outliers in the data, the way we measure firm size, or by allowing small firms’ hiring to respond differently to GDP fluctuations than large firms’ hiring, as shown in the first four columns of Table A3. In column 4, the interaction between small firm and quarterly GDP (in billions of NZD) is very close to zero and statistically insignificant; the estimate of the policy effect is essentially unchanged.

The coefficient estimate on small firm is also statistically significant, highlighting the fact that even small effects can be statistically significant when our statistical power is high. The third is an OLS regression where the dependent variable is the percentage change in employment relative to the previous month. The coefficients on between*small and post*small are again small and insignificant, suggesting a tiny 0.093% point decrease in employment growth due to the policy.

It became public knowledge that trial periods were going to be introduced for small firms 3 months prior to the first policy change, and that they would be extended to all firms 7 months prior to the second policy change, so anticipation effects are a potential concern. A firm that anticipated becoming eligible to use trial periods in the future might have postponed hiring to take advantage of trial period policy, though substantial postponement seems implausible.

Anticipation effects are not a concern for the duration of employment analysis.

If some did occur, it would cause us to overestimate the extent to which small firms increased their hiring relative to large firms between the policy changes. Given we already estimate a near-zero effect, the potential for anticipation of the second policy change by large firms does not alter our conclusions.

In addition, our baseline results are unchanged (unreported) and we see no differential hiring by period when we replicate the baseline specification for firms sized 15–24, but add to the between and post indicators an indicator for each post-announcement, pre-policy period.

Together, these results show any economy-wide increase in the number of new hires because trial period policy is tiny and economically insignificant, despite the fact that use of trial periods is fairly widespread, as discussed in Section 2.3.

5.1.3

Time-varying effects

Firms could have taken some time to learn about trial periods and how to use them after their introduction, in which case our regressions that look for one effect throughout the between-policy period would understate the true policy effect. We thus estimate a version of column 4 of the first panel of Table A1 in Appendix (including firms sized 15–24) where we allow the difference between small and large firms to differ in each 3-month period in our sample, not just in the three periods before, between, and after the policy changes.

Figure 6 plots the estimates from this regression of the discrete jump in hiring between small and large firms at each point in time, normalized to average 0 before the first policy change.

That is, we estimate the coefficient on a dummy for each 3-month period interacted with small firm, and before plotting these subtract off the average of these coefficients for the pre-period.

These estimates are all close to zero and statistically insignificant, giving further evidence of parallel trends in hiring prior to the policy changes. Furthermore, the variation around zero is similar in the between period to both before the first policy change and after the second policy change. There is no evidence that a policy effect developed over time after the first policy change.

Figure 6

Our simple theoretical model predicts that trial period policy will increase the propensity of firms to hire individuals about whom they have less information relative to individuals whose productivity they know more precisely. We expect firms to have less credible information about individuals with less recent New Zealand labor market experience, such as recent education leavers, young people, and migrants. Many workers of unknown quality are also considered disadvantaged or vulnerable in the labor market, and thus the effect of the policy on such workers is of particular interest to policymakers.

In this section, we test the policy effect on the probability a new hire is a worker of unknown quality or a disadvantaged jobseeker of various types using the same basic identification strategy. The regressions here define an observation as a hire, and the dependent variable is an indicator for the hire being of a particular type of unknown quality. Our preferred specifications are ordinary least squares (OLS) regressions, but our results are robust to using probits.

Probit results are not reported.

The controls in our preferred specification are the same as described in the previous section, with the addition of plant size (ln):

where i denotes individual, j denotes firm, k denotes industry (which is fixed over time for each firm), m denotes calendar month, r denotes level 3 industry, and t denotes month. Only new hires are potentially eligible to be hired on trial periods, so, as previously, we limit our attention to new hires at firms with 15–24 employees.

We also ran regressions that focused on rehires. Results (not presented) were very similar and all small and insignificant.

Again, we interpret the coefficient on the interaction between × small firm as the policy effect, because it shows how the difference in hiring between firms above and below the cutoff changes when trial periods are introduced for firms below the cutoff only.

For a range of definitions of risky or disadvantaged jobseekers, Table 6 presents the results of a set of linear probability regressions in which an observation is a new hire and the dependent variable is an indicator for the employee being a risky jobseeker. The types of risky job-seeker considered are: people who have received benefit income in the past year, people who have received the jobseeker benefit in the past year, people who have not received wage or salary income in the past year, migrants who had their visas approved within the past 2 years, those under 25 years old, Māori or Pasifika under 25 years old, and those who left education in the past year.

In each case, the coefficient on between*small firm is small, statistically insignificant, and precisely estimated; there is no evidence that trial periods caused firms to be more likely to hire any of these types of workers.

We also ran similar regressions for a range of other definitions of disadvantaged jobseeker: those who had benefit income in the past 2 years or the past 5 years, those with specific types of benefit income (sole parent, or supported living) in the past year, those who had not worked in the past 2 years or the past 5 years, migrants who had their visas approved in the past year or the past 5 years, and youths under 20 years old. Results (not presented) are similar.

If trial period policy did increase the probability a hire was a risky worker, we are more likely to see this effect in the industries with certain characteristics (such as high trial-period use) and firms with certain characteristics. We thus replicate our analysis of the hiring of risky workers while interacting the policy effect with various interaction variables. Key coefficient estimates are presented in Table A5 in Appendix for different dependent variables and interaction variables.

We do not find evidence of large heterogeneity in the effect on hiring risky jobseekers. For example, the first column of the first panel of Table A5 in Appendix suggests that a standard deviation increase in the trial-period use of an industry is associated with a 0.2% point increase in the policy effect on the probability of hiring a recent beneficiary (0.09 × 0.019 = 0.002). The other columns and panels tend to have similarly small point estimates.

Several point estimates are statistically significant, but they are economically small. For example, the second column of the third panel shows that a standard deviation increase in an industry’s permanent contract use is associated with a small 0.4% point increase in the policy effect on the probability a new hire is a recent jobseeker beneficiary (0.053 = 0.084). The largest estimate is the fourth column of the second panel, showing that a standard deviation increase in permanent contract use is associated with a 1% point increase in the policy effect on the probability a new hire is a recent migrant. However, the result should be interpreted with caution because the placebo test is also positive and statistically significant; comparing the between period with the post-period gives an estimated interaction effect that is 49% smaller.

Trial period policy has the potential to affect the stability of employment relationships in several ways. One concern is that it could encourage firms to take employees on for a short period, dismiss them within 90 days, and then hire replacements also for a short period. This could be detrimental to such workers, who would never acquire a measure of job security. However, if these short-term employment opportunities were additional and did not crowd out longer-term jobs, the workers might be better off than in the counterfactual where they remained unemployed.

If trial periods enabled poor employer–employee matches to end quickly, employment relationships that lasted beyond 90 days could actually be more stable subsequently than would have been the case absent trial periods.

Another risk is that trial period policy might have reduced the flexibility of the labor market by discouraging worker mobility; opponents of trial period policy argue that it could discourage people with existing jobs to move to other jobs, because if they were hired with trial periods they would lose their job security. If this effect did occur, we would expect employees who moved straight from one job to another being less likely to move to a firm that was eligible to use trial periods.

In this section, we conduct three separate pieces of analysis. We first test whether new employment relationships at trial period-eligible firms is less likely to last at least 2, 5, 12, or 24 months. We then test whether the policy affected the number of hires into longer-term positions. Finally, we test whether firms able to use trial periods hire fewer workers who come directly from prior employment.

One potential explanation for our lack of significant policy effect on essentially any of the margins we examine is that firms previously used temporary contracts to test new employees of unknown quality, and merely switched to using trial periods for this purpose when they became available. The use of temporary contracts as a method of reducing employment protection has been highlighted by Bentolila et al. (2019) in their discussions of dual labor markets. Although using temporary contracts to trial new employees is technically illegal, this may neither be well-known among employees and small employers, nor be widely enforced. If employers did use temporary contracts in this way, dismissal costs may have changed little, and we would expect trial period policy to have had little effect on firm hiring behavior. To explore the possible substitution between trial periods and temporary contracts, we use data from the 2008 and 2012 SOWL, which includes information on contract type, to look at the relationships between the types of worker–firm matches likely to involve temporary contracts pre-policy, and those likely to involve trial periods or temporary contracts post-policy.

First, we run a hire-level regression in which we regress an indicator for being hired on a temporary contract pre-policy (2008) on various employee and job characteristics. Using SOWL data from the post-period (2012), we then use these results to predict the probability each new employee would have been on a temporary contract had she been hired in the pre-period. Finally, we use this predicted probability as an explanatory variable in hire-level regressions using post (2012) data only in which the dependent variable is either an indicator for being hired on a temporary contract or an indicator for being hired with a trial period.

In the final stage regression predicting being hired on a temporary contract, a coefficient on temporary contract probability close to 1 would indicate that the types of workers being hired on temporary contracts are similar before and after trial periods were available; a coefficient much smaller than 1 would indicate a change in the use of temporary contracts. In the final stage regression predicting being hired on a trial period, a positive coefficient on temporary contract probability would indicate the characteristics that pre-policy made a worker likely to be hired on a temporary contract made him likely to be hired on a trial period post-policy. In combination, a coefficient much smaller than 1 in the final stage temporary contract regression and a positive coefficient in the final stage trial period regression would suggest a degree of substitution between trial periods and temporary contracts.

Columns 1 and 2 of Table A8 in Appendix present results from the first type of regression, showing the characteristics associated in the pre-period with a new employee being hired on a temporary contract. We use logit regressions where the dependent variable is an indicator for being on a temporary contract in 2008, and the covariates are measures of age, gender, qualification levels, and ethnicity, and in column 2 also level 1 industry and level 1 occupation fixed effects.

We use logit because the mean of the dummy dependent variable in columns 1 and 2 is around 0.2, so OLS results in a number of predicted probabilities outside the range [0,1]. However, results are similar when we instead use OLS (unreported).

The first two columns of Table 9 regress an indicator for a 2012 employee being on a temporary contract on her predicted probability of being on a temporary contract in the pre-period from either the parsimonious (column 1) or full control (column 2) model in Table A8 in Appendix. The point estimate of 1.156 in column 1 means a 10% point increase in the predicted probability of being on a temporary contract based on 2008 relationships is associated with a 15.6% point increase in the probability of being on a temporary contract in 2012; we cannot reject that this coefficient is equal to 1. Column 2 tells a qualitatively similar story. These results suggest that the characteristics associated with being on a temporary contract are similar in 2008 and 2012, i.e., before and after trial periods are available.

Columns 3 and 4 instead use as the dependent variable an indicator for being on a trial period in 2012. The coefficients estimates here are negative, large, and statistically significant. For example, column 4 suggests that a 10% point increase in the predicted probability of having a temporary contract in 2008 (based on individual and job characteristics) is associated with a 12.3% point decrease in the probability of being hired on a trial period in 2012. That is, the characteristics that made a person likely to be on a temporary contract in 2008 are strongly negatively correlated with them being hired with a trial period in 2012.

As additional verification for these results, we use a similar methodology to look at whether the characteristics that predict being hired with a trial period in 2012 predict being hired on a temporary contract in 2008. The first and second set of regressions for this analysis are given in columns 3 and 4 of Table A8 in Appendix and the columns 5 and 6 of Table 9, respectively. The point estimates of -0.270 and -0.521 in the second set are again negative and statistically significant.

Together, these results suggest the types of jobs that used temporary contracts in 2008 tended to still use temporary contracts in 2012; the types of jobs that used temporary contracts in 2008 did not tend to use trial periods in 2012; and the types of jobs that used trial periods in 2012 did not tend to use temporary contracts in 2008. These results are inconsistent with temporary contracts in 2008 being used extensively to trial new employees and subsequently being replaced by trial periods in this purpose.

This is also consistent with estimated aggregates from the 2008 and 2012 Survey of Working Life; a higher proportion of jobs were on temporary contracts in 2012 than 2008, despite trial periods not being available in 2008. It is difficult to reconcile this with a story of widespread crowding-out of temporary contracts due to trial periods. Although we note that the surveys are not completely comparable because the 2008 survey was in March while the 2012 survey was in December. December is the summer season in New Zealand, with many temporary workers.

Our empirical strategy provides the cleanest identification of the policy effect for firms with nearly 20 employees. However, one possibility is that very small firms (or very large firms, though this is less likely to be the case) were affected more by trial period policy than were firms with nearly 20 employees. Human resource costs related to hiring and dismissals are generally more of a burden for smaller firms, so it is a plausible hypothesis that very small firms were affected more by the policy. Our main specifications do not estimate the effect on firms with fewer than 15 employees. However, we run several robustness checks where we attempt to identify the policy effect on smaller firms. First, we expand the firm size range in our regressions out to 10–50 employees. Second, we expand the size range from 1 to 29 employees, and replace our small firm dummy and its interactions with a set of indicator variables for the size bands in this range (1–4, 5–9, 10–14, 15–19, and 25–29, omitting the category 20–24) and their interactions. None of these regressions suggest a significant policy effect on small firms, though the evidence they provide should thus be interpreted as suggestive only.

There are several ways in which the hiring behavior of treated (small) firms could affect the hiring behavior of control (large) firms that should be borne in mind when interpreting our results. These arise from the fact that both types of firms hire from the same pool of jobseekers. Supposing the first policy change caused small firms to increase their hiring, the additional workers hired by small firms would therefore not be available to be hired by large firms. This could actually decrease hiring by large firms if other jobseekers were not perfect substitutes for those who were made unavailable by the policy. Over several years of elevated hiring by small firms, this effect could have been accentuated.

Through a similar mechanism, if small firms increased their hiring substantially soon after the first policy change, they could have depleted the pool of desirable jobseekers, causing their own hiring at a later date to be lower.

All these potential mechanisms suggest that control firms may have actually been treated by the first policy change in a way that would cause us to overestimate the effect of the policy on treated firms. However, the magnitude of any of these effects on large firms is likely to be much smaller than the policy effect on small firms, so should not be of material importance in the absence of very large policy effects on small firms. In practice, we find policy effects close to zero throughout the article.

Finally, our regressions that investigate quantity of hiring test for an effect of the policy on number of monthly hires for a firm of given size. Supposing the policy instead caused a onetime increase in firm size, our analysis may not be able to pick up this effect.

Although Figure 6 does not suggest this was the case because it does not shown even a short-term increase in quantity of hiring.