# Research Discussion Paper – RDP 2020-07 How Many Jobs Did JobKeeper Keep?

## 1. Introduction

The COVID-19 outbreak in Australia in early 2020 led to a sharp fall in economic activity. In response, the Australian Government announced a series of measures to support incomes and employment. The largest single measure was the $101.3 billion wage subsidy scheme called the ‘JobKeeper Payment’. As its name implies, a key objective of the JobKeeper Payment was to preserve the connections between employers and their employees during the crisis, and to support business and job survival. It did this by giving employers a wage subsidy for eligible employees in order to help them retain those employees and reduce the associated wage costs. Another objective of JobKeeper was to provide income support. In the initial six-month stage of the program (30 March 2020 to 27 September 2020), which is the focus of our paper, the subsidy was paid as a flat$1,500 per fortnight for each eligible employee.

The JobKeeper Payment is one of the largest labour market interventions in Australia's history (Australian Government 2020b). In its first six months, it supported around 3.5 million workers in more than 900,000 businesses, and undoubtedly played a crucial role in cushioning the decline in employment and incomes over the first half of 2020.[1] The Treasury's (2020b) three-month review of the program used descriptive evidence to make the assessment that JobKeeper has had a material effect. To date, however, no study has estimated the causal effect of the subsidy on employment using an approach that accounts for the differences between workers who received JobKeeper and those who did not. For this reason, the effect of JobKeeper on employment remains an open question. Our paper helps to fill this gap in the evidence base.

Specifically, we seek to answer the following question: what effect did JobKeeper have on employment during the first four months of the program? In doing so, we provide the first quantitative estimates of the causal effect of JobKeeper on employment, which build on the descriptive evidence discussed by Treasury (2020b). Our goal is to estimate the counterfactual – that is, how much employment would have fallen in the absence of JobKeeper. We find that one in every five employees who received JobKeeper would have exited employment had it not been for the wage subsidy. Scaling our estimates up to the aggregate level suggests that JobKeeper reduced overall employment losses by at least 700,000 during its first four months (Figure 1). While our error bands are wide and our analysis has a number of important caveats, our findings are close to Treasury's ex post and ex ante estimates of the number of jobs that the program ‘saved’.

To identify the causal effect of JobKeeper on employment, we make use of a strict threshold in the eligibility criteria for the program. We compare the employment outcomes of casual employees who had a little less than 12 months of tenure with their employer in early March (who narrowly missed out on being eligible for JobKeeper) to that of casuals with a little more than 12 months of tenure (who were potentially eligible). Because our approach focuses on casual employees in a narrow range of tenure, these two groups should be similar in terms of their observable and unobservable characteristics. As such, any differences between these groups that emerged after the introduction of JobKeeper can be attributed to the effects of the program rather than to other factors, such as the uneven effect of COVID-19 across industries. To implement this approach, we use individual-level data from the Labour Force Survey (LFS) and a difference-in-differences strategy.

Our findings have implications for policy. First, a better understanding of the effects of JobKeeper on employment can provide additional guidance to policymakers on the benefits of extending (or costs of withdrawing) the scheme. While we do not perform a cost-benefit analysis, our results would be an important consideration in such an analysis. Second, our results will be useful for forecasters grappling with the question of whether the withdrawal of existing support measures in late 2020 and early 2021 will have implications for labour market outcomes and economic growth. For example, it may be reasonable to assume that the number of jobs saved by the introduction of JobKeeper provides an upper bound on the number of jobs that will be lost once the program ends. In saying that, any such employment losses could be offset by an underlying recovery in economic activity or further policy stimulus. It is reasonable to think that the effects of JobKeeper on employment will vary with the state of the labour market, and could plausibly be much lower by the time the scheme ends. Finally, as Treasury (2020b, p 39) have noted, a better understanding of the effects of JobKeeper can aid policymakers in the event of future economic shocks.

Throughout this paper we pay close attention to the assumptions that underpin our results. There are two that are worth emphasising upfront, because we were not able to test them in a rigorous way. The first of these key assumptions is that JobKeeper did not have spillover effects on workers who did not receive it, either at a firm level (for example, through its general support of firm profitability) or at an aggregate level via general equilibrium effects (for example, through its effect of supporting the overall strength of the economy). If this assumption does not hold, we may have either overstated or understated the effects of JobKeeper on employment depending on the nature of the spillover. The second key assumption is that the effects we estimate for casuals with limited job tenure can generalise to other JobKeeper recipients. That is, we assume that JobKeeper had similar effects on employment outcomes for casual employees as for permanent ones, notwithstanding that these employment relationships differ in a range of ways, as do the characteristics of the firms and workers who use them.

It is important to note that our analysis is entirely retrospective. Our focus is on how JobKeeper supported employment in the first few months of the program. We do not consider the effects of JobKeeper from August 2020 onwards. Notably, the changes in payment rates and eligibility that occurred from end September mean that our estimates may not generalise beyond our period of analysis. Treasury (2020b, p 7) has noted that JobKeeper has a ‘number of features that create adverse incentives which may become more pronounced over time as the economy recovers’.

An important policy question is whether JobKeeper was effective in alleviating the longer-run effects of labour market scarring. We do not consider this question in our paper. Even once the data become available, analysing these longer-run effects will be a more complicated task given the broader range of competing forces at play. An important avenue for future research will be to study the longer-term benefits and costs of the program on employment, earnings and productivity.

Another aspect of JobKeeper that our study does not consider explicitly is the role the program played in supporting incomes of firms and workers, which was one of its main objectives. As noted above, our analysis is also silent on the various indirect channels through which JobKeeper may have affected economic outcomes and employment in the first few months of the program, such as via second-round effects on aggregate demand. By focusing on the direct employment effects alone, our analysis provides a partial, albeit important, evaluation of the scheme.

The remainder of this paper is structured as follows. Section 2 provides some background on the JobKeeper Payment. Section 3 briefly discusses the existing evidence on JobKeeper and previous work on wage subsidy schemes. The data and empirical strategy are described in Sections 4 and 5. Sections 6 and 7 present the results and robustness tests. Section 8 provides our assessment of the short-run effect of JobKeeper and Section 9 provides some concluding remarks.

## 2.1 Background

The outbreak of COVID-19 infections, along with the measures used to contain the spread of the virus, led to a sharp contraction in economic activity in Australia from around mid March 2020. The Australian Government responded by announcing a series of economic support packages in mid-to-late March. The single largest measure was the JobKeeper program, which provided a wage subsidy for businesses significantly affected by COVID-19 to help them retain and continue to pay their staff.

JobKeeper was announced on 30 March 2020 (effective immediately), and was originally scheduled to run for six months until end September 2020. The program had three objectives:

1. to support business and job survival
2. to preserve the employment relationship between employers and their workforce
3. to provide income support to business owners and their workforce.

Our paper focuses on the second of these objectives (and, to a lesser extent, the first). Our study does not consider how effectively the program achieved its third objective of providing income support.

Although the program was originally due to end in September 2020, in July the government announced an extension until March 2021, albeit with some modified eligibility criteria and downward adjustments to payment rates (‘JobKeeper 2.0’). There were some further modifications announced in August in response to the increased social distancing restrictions in Victoria (Morrison and Frydenberg 2020). We do not study the effects of these changes or JobKeeper 2.0 in our paper. Instead, the focus of our paper is on the first four months of the program. In the remainder of our paper, any references we make to ‘JobKeeper’ or the ‘JobKeeper Payment’ will be referring specifically to this initial phase unless indicated otherwise.

## 2.2 Design Features

Under JobKeeper, eligible businesses were given a wage subsidy of $1,500 per fortnight for each eligible employee in order to help them retain those employees and reduce wage costs.[2] More specifically, eligible businesses that made wage payments of at least$1,500 per fortnight to an eligible worker were reimbursed that $1,500 amount in full by the Australian Taxation Office (ATO).[3] There are several aspects of this payment design that warrant further discussion. First, the subsidy was paid as a flat per-worker rate: the value of the subsidy was the same for all covered workers regardless of the number of hours they worked during the program or their earnings. This flat rate distinguishes the JobKeeper Payment from the wage subsidy schemes used in most other OECD countries, which pay covered employees a proportion of their pre-scheme earnings up to a cap (RBA 2020).[4] Second, the$1,500 payment rate also acted as a wage floor. If an eligible employee had been earning less than $1,500 per fortnight prior to the COVID-19 crisis, their employer needed to increase their wage payment to the$1,500 floor under the program.[5] This meant that many part-time employees were entitled to higher payments under JobKeeper than they would ordinarily receive.

## 8.1 Aggregate Effects

Our baseline estimate is that receiving JobKeeper increased an employee's probability of remaining employed by about 20 percentage points. We can, thus, estimate the aggregate effect of the wage subsidy on employment by multiplying this estimate (0.2) by the number of people on JobKeeper during our period of analysis (around 3.5 million). This back-of-the-envelope calculation suggests that JobKeeper reduced the aggregate fall in employment over the first half of 2020 by at least 700,000.

To put this estimate into perspective, the actual fall in employment over the first half of 2020 was 650,000. As such, our estimates imply that overall employment losses would have been twice as large over this period without JobKeeper. Our estimate of the no-JobKeeper counterfactual – which subtracts our estimates of the employment saved by JobKeeper from the actual level of employment – was shown in Figure 1, along with its 95 per cent confidence interval.[40]

Our estimate is similar to Treasury's initial estimate that the unemployment rate would be around 5 percentage points higher in the absence of JobKeeper.[41] A 5 percentage point reduction in the unemployment rate equates to at least 700,000 fewer people leaving employment.[42] Our estimate is a little larger than Treasury's more recent estimate in the July Economic and Fiscal Update that all of the fiscal stimulus has prevented the loss of around 700,000 jobs (Australian Government 2020b, p 38). The latter estimate also includes support measures other than JobKeeper, such as cash payments to households, income support and investment incentives for businesses, loan guarantees and regulatory measures, so it could be interpreted as an upper bound estimate of JobKeeper's effect.

We have characterised our estimate of the aggregate effect as being ‘at least 700,000’, rather than ‘around 700,000’ for a few reasons. First, our baseline estimates for May, June and July are 696,000, 1,002,000 and 839,000, respectively. Second, JobKeeper is likely to have had positive second-round effects on employment, by supporting incomes. Our approach does not capture these general equilibrium effects. In saying that, we cannot rule out the possibility that we have overstated the aggregate effects of JobKeeper on employment; for instance, if the employment effects were smaller for permanent employees than for casuals (see Section 8.3 below) or if our estimates are biased upwards for reasons discussed in Section 7.2.

## 8.2 Cost per Relationship Saved

The first phase of JobKeeper provided $70 billion in support over a six-month period (30 March to 27 September). If we combine this with our estimate of the effect of the program on employment – and if we assume that the effects we estimated for April to July were similar in August and September – it suggests each employee-employer relationship saved by JobKeeper cost$100,000 (= $70b ÷ 700,000) over the six-month period. This simple measure of the cost-effectiveness of JobKeeper appears to compare favourably to similar programs in other countries, such as the PPP in the United States which has an estimated cost-per-job saved of US$224,000 (Autor et al 2020). This may reflect that the JobKeeper scheme was more tightly targeted than the PPP (Hamilton 2020).

However, there are several differences between JobKeeper and the PPP that make comparisons difficult (see Table A1 and Hamilton (2020) for a summary of these differences). In particular, the JobKeeper funds were dispensed to firms reasonably uniformly over a six-month period. In contrast, PPP funds were provided to firms upfront (as a forgivable loan) and firms had some discretion over how quickly to dispense those funds to payrolls over time, which means the duration of the PPP is less clear.[43] While this makes it hard to adjust the cost-per-job-saved metrics for differences in program duration (e.g. by comparing the monthly-cost-per-job saved of the programs), this adjustment would likely tilt the comparison more strongly in favour of JobKeeper. This is because funds appear to be less frontloaded under JobKeeper than under the PPP.

However, any cost-benefit analysis of JobKeeper is well beyond the scope of our paper. We leave that analysis for researchers and analysts with expertise in that area.

## 8.3 Casual versus Permanent Workers

A key assumption behind our estimates of the aggregate effects of JobKeeper is that the treatment effects we estimate for casuals with 6–23 months tenure can generalise to other JobKeeper recipients.

Our treatment effect estimates represent local treatment effects around the tenure-eligibility threshold. It is possible that JobKeeper had a different effect on casuals away from the tenure threshold. For example, longer-tenured casuals (with, say, more than two years of tenure) are likely to have accumulated more firm-specific human capital on average than their shorter-tenure colleagues and thus may have been less likely to lose their job in the absence of JobKeeper. In this case, our estimates of the aggregate effect of JobKeeper would be overstated, all else being equal.

Whether our treatment effect estimates can generalise to permanent employees is even more uncertain. In a casual employment relationship, an employee does not have guaranteed hours of work, and the relationship can be ended without notice (FWO 2020a). In a permanent relationship, an employee has an advance commitment from their employer about hours of work and length of service, and are generally entitled to notice before termination. Unlike permanent employees, casual employees are also generally not entitled to paid annual and sick leave from their employer.[44]

Whether the employment outcomes of permanent employees responded differently to casual employees to receiving JobKeeper is a priori unclear. On the one hand, the higher firing costs associated with permanent employment (relative to casual work) may have meant that permanent employees on JobKeeper were less likely to be dismissed in the absence of the program.[45] In that case, our estimates would overstate the effects of JobKeeper on aggregate employment. However, we provide evidence in Appendix D suggesting that firing costs (specifically, redundancy payments) had no discernible effect on employment outcomes during the initial months of the COVID-19 crisis. Employment of permanent workers may also have responded less than casuals to JobKeeper in view of the fact that the $1,500 fortnightly payment represented a larger fraction of average pre-scheme earnings for casual workers than for permanent workers (i.e. a higher replacement rate), reflecting the lower average pre-scheme earnings of casual employees.[46] On the other hand, the temporary changes to the Fair Work Act 2009 to provide firms with more flexibility to modify employees' working arrangements may have had a larger employment-preserving effect on permanent staff than casuals. As discussed earlier, these changes meant that an employee covered by JobKeeper could have their hours reduced, or be redeployed, at their employer's discretion. This flexibility was already a feature of most casual arrangements, but not permanent ones. As such, the JobKeeper Payment program – broadly defined to include both the subsidy and the flexibility provisions – may have had a larger effect on employment of permanent workers than casuals.[47] Teasing out the separate effects of the wage subsidy and the flexibility provisions is an avenue for future work. While our main identification strategy is restricted to casual employees, our alternative strategy based on the residency requirement captures the effects of JobKeeper on both casual and permanent employees. Using this alternative approach, we can perform a test of the hypothesis of constant treatment effects across casual and permanent employees (see Appendix E for details). We do not reject the hypothesis of equal treatment effects across groups at conventional levels of significance. While this suggests that the assumption of equal treatment effects across casual and permanent employees may be reasonable, this test suffered from low power due to small sample sizes. Our approach to inferring aggregate effects also generalises our treatment effect estimates to non-employees. Under JobKeeper, self-employed people could receive the$1,500 payment as a ‘business participant’ if they were an eligible sole trader, partner, beneficiary of a trust, or were actively engaged in an eligible entity as a shareholder or director. In this situation eligibility was based on the firm-eligibility test and some other criteria. Non-employing businesses made up around 11 per cent of all individual JobKeeper recipients in April (Treasury 2020b). By extrapolating our treatment effect estimates from Section 6.2 to the self-employed, we are implicitly assuming that one-fifth of all self-employed JobKeeper recipients would have exited employment in the absence of JobKeeper. We cannot test this assumption directly, so we leave it as a caveat and avenue for future research.

## 9. Conclusion

We find that JobKeeper played an important role in cushioning the decline in employment over the first half of 2020. Our baseline estimate is that one in five JobKeeper recipients would not have stayed employed during this period had it not been for JobKeeper. At the aggregate level, this implies JobKeeper prevented at least 700,000 additional employment relationships being lost in the short term. Overall employment losses would have been twice as large over the first half of 2020 without JobKeeper.

We have emphasised several important assumptions underlying our estimates. These assumptions should be kept in mind, and further work using administrative data sources should be undertaken to confirm our results.

Our analysis is retrospective and short-term in focus. We examine the extent to which JobKeeper supported employment in the first four months of the program. We do not consider the employment effects from August onward (including JobKeeper 2.0), or the effectiveness of the program in alleviating the longer-run effects of labour market scarring. Policymakers should not assume that the short-term effects of the scheme will necessarily persist. Indeed, the international literature suggests that wage subsidies, if maintained too long, can have adverse effects on incentives and impede the reallocation of labour.

A key objective of JobKeeper was to provide income support to business owners and their workers. We do not study this important aspect. Our analysis is also silent on the various indirect channels through which JobKeeper may have affected economic outcomes, such as via second-round demand effects. These general equilibrium effects are not captured in our estimates. By focusing on the direct employment effects alone, our analysis provides a partial, albeit important, evaluation of the scheme.

## Appendix A: Comparison of PPP and JobKeeper Programs

Table A1: Comparison of PPP and JobKeeper Programs
Autor et al (2020) Paycheck Protection Program Bishop and Day JobKeeper Payment (initial six months)
Details of program
Structure Forgivable loans issued by banks and guaranteed by the US government Direct subsidies for payroll costs implemented by ATO
Replacement rate Proportionate to pre-scheme payroll (100%, but with US$100,000 cap for each worker) Varies based on worker's pre-scheme earnings Generosity 2.5 × the firm's pre-COVID-19 monthly payroll expenses up to a maximum of US$10m A$1,500 per eligible employee per fortnight (also wage floor) Duration Funds cover 10 weeks of payroll; 60% of funds must be spent on payroll over 24 weeks; headcount/compensation tests apply on 31 Dec 2020 26 weeks Start date 3 Apr 2020 30 Mar 2020 Cost US$518b (2.4% of 2019 GDP), as of 17 Jul 2020 A$70b (3.5% of 2019 GDP) Firm eligibility Firm had 500 or fewer employees (higher threshold for some industries) Firms experienced a specified revenue loss that depended on their size Worker eligibility na Australian resident employed at eligible firm on 1 Mar 2020; minimum of 12 months of tenure for casuals Conditions (for loan forgiveness or payment of subsidy) The amount of the loan used for payroll costs, rent, utilities and interest during the 24-week period (initially 8 weeks) after loan origination is forgiven, provided that 60% (initially 75%) of the amount forgiven is spent on payroll and the firm does not reduce headcount relative to pre-crisis levels or reduce any employee's compensation by more than 25% of their pre-crisis level(a) The firm pays all eligible workers at least A$1,500 per fortnight for the duration of the firm's participation
Details of evaluation
Period of evaluation Apr–Jun Apr–Jul
Outcome variable Firm-level employment (paid jobs) Probability employee was employed (ABS definition)
Unit of analysis Firms; those close to the size eligibility threshold (500 employees) Casual employees; those close to the worker-eligibility threshold (12 months)
Data Administrative panel data from a large payroll processing firm (ADP) Survey panel data from LFS
Identification Exploit firm-size eligibility cut-offs; compare firms above and below the cut-off using difference-in-differences Exploit tenure-eligibility cut-offs; compare workers above and below the cut-off using difference-in-differences
Results of evaluation
Effect of program eligibility 3.25%(b) 7–10 ppt
Take-up rate (share of eligible population that participated) 67%
(midpoint of 62–72% range)
33%
Treatment effect on treated 4.85% 20–30 ppt
Aggregate employment effect 2.31m 0.7m
Cost-per-job saved US$224,000 (2.31m ÷ US$518b) A$100,000 (0.7m ÷ A$70b)

Notes: (a) PPP loans allow employees to be furloughed and rehired before 31 December 2020 and remain eligible for loan forgiveness; share of loan forgiven is reduced proportionately if headcount/compensation are reduced beyond these levels
(b) Autor et al's preferred central tendency estimate

Sources: Authors’ calculations; Autor et al (2020)

## Appendix B: Additional Details on the Model

Equation (2) gives the effect of JobKeeper worker eligibility on employment, which is different to the effect of actually receiving JobKeeper on employment. In Section 6.2 we mentioned that we can obtain an estimate of the latter by applying a scaling factor to the former. In this appendix we discuss this scaling approach in detail. To do this, we start by describing the ‘ideal model’ that we wish that we could estimate, but are unable to given the limitations of the data we have access to.

## B.1 The Ideal Model

Ideally we would directly estimate the effect of receiving JobKeeper on the probability of being employed in month j, for those people who were employed on 1 March 2020 (the eligibility date for JobKeeper),

(B1) $E i,j =p+τJobKeepe r i +φΔRevenu e i,f,j + ω i,j$

where JobKeeperi equals one if worker i was participating in the JobKeeper program at time j, and zero otherwise. A key control is $\text{Δ}$Revenuei,f,j which measures the COVID-19-related revenue loss experienced by the firm f that employed worker i on 1 March 2010 (in cumulative terms to month j). The parameter of interest is $\tau$ , which is the effect of JobKeeper on the probability of being employed in period j, controlling for the revenue shock that the firm experienced during the crisis.[48]

The first thing that prevents us from estimating the ideal model is that we do not observe firm revenues in our dataset. If this were the only missing variable, we could feasibly estimate the following model,

(B2) $E i,j =ρ+τJobKeepe r i + ψ i,j$

However, if we leave $\text{Δ}$Revenuei,f,j out of the model as in Equation (B2), the estimate of $\stackrel{^}{\tau }$ would be biased, because receiving JobKeeper is correlated with firm revenue losses due to the firm-eligibility test. Formally, $\mathrm{cov}\left(JobKee{p}_{i},{\psi }_{i,j}\right)=\phi \mathrm{cov}\left(JobKeepe{r}_{i},\text{\hspace{0.17em}}\text{Δ}Revenu{e}_{i,f,j}\right)\ne 0.$

## B.2 A Feasible Model

We can overcome the omitted variable bias in Equation (B2) by instrumenting for JobKeeperi and focusing on casuals with 6–23 months of tenure. An obvious instrument in this case is our dummy variable for whether the worker passed the 12-month tenure test for casuals, Eligi. This instrument is relevant (positively correlated with receiving JobKeeper) and exogenous (unrelated to $\text{Δ}$Revenuei,f,j). Our decision to focus on a narrow range of job tenure can be motivated using this exogeneity assumption. If we included a broader range of tenure it would raise the likelihood of there being some unobservable factor correlated with both the likelihood of receiving JobKeeper and firm revenue losses.

In addition to accounting for omitted variables, this instrumental variables (IV) approach also gives us a way of estimating the parameter that policymakers are most interested in – namely, the effect of JobKeeper on workers who received JobKeeper. This is the case even though we do not have a direct measure of whether a person received JobKeeper in our dataset. To see this, note that the set-up with a binary treatment and binary instrument lends itself to the Wald IV estimator:

$τ IV = cov( E i,j , Eli g i ) cov( JobKeepe r i , Eli g i ) = E( E i,j | Eli g i =1 )−E( E i,j | Eli g i =0 ) E( JobKeepe r i | Eli g i =1 )−E( JobKeepe r i | Eli g i =0 )$

Casual employees cannot access JobKeeper if they do not satisfy the tenure test, so this simplifies to:

(B3) $τ IV = E( E i,j | Eli g i =1 )−E( E i,j | Eli g i =0 ) E( JobKeepe r i | Eli g i =1 )$

The numerator of Equation (B3) is the effect of JobKeeper worker eligibility on employment. This is an intent-to-treat effect. We can estimate this effect using the LFS micro data since we observe information on whether the worker is employed on a casual basis and whether they have been engaged long enough to satisfy the 12-month tenure rule. Our estimate of the numerator in Equation (B3) is our estimate of $\stackrel{^}{\delta }$ from using OLS on Equation (2) (a linear probability model).

The denominator of Equation (B3) is the probability of receiving JobKeeper, conditional on being worker-eligible. This quantity cannot be estimated using the LFS micro data alone since we do not observe who receives JobKeeper. However, we can construct an estimate using a combination of ATO data and the LLFS:

(B4) $E( JobKeepe r i | Eli g i =1 )≈ total JobKeeper recipients no of workers satisfying worker eligibility ≈ 3.5m ∼10.26m ≈ 1 3$

Total JobKeeper recipients is from official sources based on administrative data (3.5 million over the April to May period according to Treasury (2020b)), while the total number of workers satisfying the worker-eligibility test is our estimate based on LFS micro data for February 2020. To obtain this estimate, we take the total number of employed people and subtract the number of casual employees with less than 12 months of job tenure. We also subtract people employed in the public sector or by a major bank, who are ineligible.[49]

Our estimate of E(JobKeeperi|Eligi = 1) from Equation (B4) is imperfect since it pertains to a broader population than what we use to estimate the intent-to-treat effect in Equation (B3).[50] The premise of the Wald estimator is that the numerator and denominator are drawn from the same population. The difficulty in doing this is that we do not receive sufficiently granular administrative data on the characteristics of individuals receiving JobKeeper. One dimension that we do have disaggregation in official JobKeeper numbers is by industry. As a robustness check, we examined whether our estimates were robust to stratifying the calculation of E(JobKeeperi|Eligi = 1) by industry, which accounts for any differences in industry composition between our estimation sample for Equation (B3) and the broader population of worker-eligible individuals.[51] This industry stratification had no material effect on our results; our estimate of E(JobKeeperi|Eligi = 1) is still close to ⅓.

The above discussion suggests that to obtain an estimate of the causal effect of JobKeeper on employment we can simply estimate Equation (2) using OLS and then divide the estimate of $\stackrel{^}{\delta }$ by a scaling factor of ⅓,

(B5) $τ ^ IV = δ ^ 1 3$

We do this calculation in Section 6.2. We calculate standard errors for ${\tau }_{IV}$ under the simplifying assumption that $\delta$ is random but E(JobKeeperi|Eligi = 1) is known. This does not account for the sampling variance of the scaling factor, which means our standard errors for ${\stackrel{^}{\tau }}_{IV}$ are likely to be too small.

Our estimate of ${\tau }_{IV}$ yields the average treatment effect on the treated (ATT). That is, it tells us the average causal effect of receiving JobKeeper on employment for those who actually received the subsidy.[52] For this reason, our estimates only pertain to the effects of JobKeeper on people working at eligible firms.

## B.3 Implied Aggregate Effect

To estimate the implied effect of JobKeeper on aggregate employment in Section 8.1 we use the following formula,

Total employment effect $={\stackrel{^}{\tau }}_{IV}×3.5\text{m}$

Or, equivalently

Total employment effect $=\stackrel{^}{\delta }×10.26\text{m}$

Autor et al (2020) use a similar calculation to estimate the aggregate effect of the PPP on US employment.

## Appendix C: Additional Statistics and Results

Table C1: Descriptive Statistics for Casual Sample versus Other Employees
Sample means
Control group (February tenure: 6–10 months) Treatment group (February tenure: 12–23 months) All casual employees All employees
Industry (%)
Agriculture, forestry & fishing 2.2 2.7 3.8 1.9
Mining 1.8 1.3 1.5 2.7
Manufacturing 5.1 3.4 5.4 9.0
Electricity, gas, water & waste 0.7 0.8 0.7 1.0
Construction 4.4 5.8 7.2 8.5
Wholesale trade 1.1 1.6 2.0 3.5
Retail trade 18.2 20.2 16.7 12.0
Accomm & food services 24.5 23.1 19.9 7.9
Transport, postal & ware 7.7 6.9 6.2 5.7
Info media & telecom 1.5 0.5 1.3 2.0
Finance & insurance 0.4 0.3 0.4 2.8
Rental, hiring & real estate 1.1 2.4 1.7 1.9
Prof, scientific & tech services 5.5 3.4 4.7 9.4
Admin & support services 5.1 4.0 4.8 3.5
Public admin & safety 0.0 0.0 0.0 0.1
Education & training 2.2 5.6 5.3 9.2
Health care & social assistance 10.6 10.9 11.2 12.8
Arts & recreation 2.9 4.8 3.6 2.1
Other services 5.1 2.4 3.5 3.9
Occupational skill level 4.0 4.0 3.8 3.0
(1 = highest, 5 = lowest)
Hours worked 21.8 21.4 22.5 32.6
One job only (%) 92.0 90.7 90.8 93.9
Student (%) 36.5 41.9 31.6 16.6
Age (years) 31.0 31.5 35.5 40.1
Female (%) 50.7 50.1 53.0 48.4
Recent migrant (%) 12.0 9.8 7.8 5.1
Observations 274 377 2,305 8,951

Note: Characteristics in February for sample remaining in June 2020

Sources: ABS; Authors' calculations

Table C2: Regression Results for Equation (2)
Month by month estimation
Constant $\left(\stackrel{^}{\sigma }\right)$ Difference-in-differences
estimate $\left(\stackrel{^}{\delta }\right)×100$
Sample size
November 2019 0.95***
(0.01)
−1.62
(1.56)
889
December 2019 0.96***
(0.01)
−1.10
(1.23)
1,076
January 2020 0.93***
(0.01)
−0.21
(1.47)
1,311
February 2020 na na 1,604
March 2020 0.94***
(0.01)
0.32
(1.34)
1,272
April 2020 0.79***
(0.02)
−0.91
(2.54)
1,050
May 2020 0.67***
(0.02)
6.78**
(3.18)
847
June 2020 0.70***
(0.03)
9.77***
(3.46)
651
July 2020 0.75***
(0.03)
8.18**
(3.91)
462

Notes: ***, **, and * denote statistical significance at the 1, 5, and 10 per cent levels, respectively; robust standard errors in parentheses

Sources: ABS; Authors' calculations

## Appendix D: Robustness Checks

Like any analysis using difference-in-differences, our results are sensitive to violations of the parallel trends assumption. As discussed in Section 5.2, the main way we address this assumption is to focus on fairly narrow tenure windows around the 12-month cut-off. In this appendix, we discuss the results of several robustness tests that address other concerns about violations of this assumption.

## D.1 Pre-trends

Our first robustness test is to examine the employment trends in the treatment and control group leading up to the JobKeeper program. These trends for the period November 2019 to February 2020 are shown in Figure 2. We find that the employment trends were similar in the lead up to the program, with the 95 per cent confidence intervals for the difference-in-differences estimates for these periods spanning zero. This gives more confidence that the parallel trends assumption holds.

In saying that, in our set-up the pre-trends provide a weaker test of the parallel trends assumption than in some other contexts, because the treatment and control groups are restricted to people employed in February 2020 with at least six months of job tenure. As such, employment trends prior to February primarily reflect nuances in the definition of employment (see Section 5.5) rather than job creation and job destruction. For example, the 7½ per cent of people in the treatment and control groups who were not employed in January (Figure 2) will reflect those away from their job on unpaid leave for 4 weeks or longer over the summer holiday period, who are classified as not ‘employed’.

## D.2 Controls

Our second robustness test is to examine whether our baseline results are robust to adding controls. Controls include dummies for industry of employment, occupational skill level, sex, migrant status, student status, multiple-job holding status, and a quadratic in age. All controls are measured in the pre-treatment period (February 2020), but are allowed to affect subsequent employment outcomes. For example, working in the accommodation & food industry in February is allowed to have an effect on a person's employment status in June and therefore accounts for the lingering effect of the lockdowns and social distancing on cafés. Adding these controls has no material effect on our results, which provides further confidence that parallel trends holds. This finding is not too surprising given our earlier finding that the treatment and control groups are balanced on observable factors (Table 1).

## D.3 Placebo Tests Using Data from Earlier Periods

Our third robustness test is designed to tease out whether our baseline results are driven by higher turnover for the shorter-tenure casuals relative to longer-tenure ones, either in general or as part of a seasonal pattern. To do this, we look for evidence of a ‘placebo effect’ in an earlier period – here, the corresponding period of 2019. There is no evidence of a placebo effect; in 2019 employment losses of longer-tenure casuals were similar to shorter-tenure casuals (Figure D1, middle panel). In other words, underlying differences in turnover rates are not driving our results.

Unfortunately, the variable for the employee's status in employment (i.e. whether casual, permanent or self-employed) is only available in the LLFS from August 2014 onwards, which means we cannot not do a similar placebo test for the last major downturn – namely, the GFC in 2008–09.

## D.4 Tenure Gradient in Employment Losses for Short-term Casuals

We also examined whether our baseline results are driven by last-in-first-out (LIFO) practices some firms may have used to prioritise dismissals during COVID-19. Specifically, longer-tenure casuals may have been more likely to retain their job than shorter-tenure casuals in the absence of JobKeeper, if firms tend to be more likely to dismiss their shorter-serving staff before their longer-serving staff during a downturn. Our baseline approach tries to circumvent this issue by restricting the estimation sample to a narrow range of tenure around the 12-month threshold. But for efficiency and data reasons, we still needed to include some people with modestly more tenure than others in our sample. The presence of LIFO practices may lead us to overstate the effect of JobKeeper on employment.

We test for this potential bias by examining whether short-term casuals with very short tenures (e.g. 1 or 2 months) in February 2020 were more likely to lose employment over the May to July period than short-term casuals with longer tenures (e.g. 9 or 10 months). To do this, we regress employment in a given month (say, July 2020) on the worker's tenure in their main job (a continuous variable) in February 2020. We do this for a sample of workers who were employed on a casual basis with between 1 and 10 months of tenure in February. All people in this group were ineligible for JobKeeper, so a positive and statistically significant ‘tenure gradient’ in employment would be evidence of LIFO practices. We find no statistically significant tenure gradient in May, June or July; indeed, in June and July the coefficient on the tenure variable has a negative sign, suggesting that, if anything, workers with more tenure were slightly less likely to remain employed than those with less tenure.[53]

## D.5 Placebo Tests Using Non-casual Employees

We can also test for the presence of LIFO practices by looking at how employment rates of non-casual workers changed around the same tenure level as in our baseline approach. This is a useful exercise because non-casual workers are not subject to the 12-month tenure rule under JobKeeper, which means that any divergence in employment rates of non-casual workers around this threshold must be due to something other than the effects of JobKeeper, such as LIFO practices. We do not see any meaningful differences in the employment rates for non-casual employees with 6–10 months of tenure (in February 2020) relative to those with 12–23 months of tenure (Figure D1, right-hand panel). We take this as further evidence that any LIFO practices are not driving our baseline results.

The results of this placebo test also shed light on the role of firing costs, which can influence a firm's decisions to dismiss an employee when conditions deteriorate. In Australia, permanent employees are eligible for redundancy pay (a key component of firing costs) after 12 months of continuous service at a firm (FWO 2020c).[54] This means our placebo test using non-casual workers can be interpreted as a test both for LIFO effects and/or for the effects of higher firing costs on worker turnover (both effects are expected to operate in the same direction). As such, another interpretation of the placebo test result is that differences in firing costs are not important for explaining differences in employment outcomes across workers during the first few months of the COVID-19 crisis. Permanent employees eligible for redundancy pay did not have lower rates of job loss than those without it (Figure D1). However, this interpretation is muddied somewhat because the 12-month threshold for redundancy pay-eligibility is not anchored at a fixed point in time (unlike the threshold for JobKeeper eligibility which was anchored at 1 March), which means that some of the lower-tenure group became eligible for redundancy pay during the April to July 2020 period.

## D.6 Excluding Multiple-job Holders

Our final robustness test is to examine if our results are sensitive to excluding multiple-job holders from the estimation sample. As discussed in Section 5.5, some individuals in our sample held more than one job prior to JobKeeper, but each person could only receive JobKeeper from their primary employer. Around 9 per cent of our treatment and control groups held more than one job in February 2020 (Table 1). In our baseline approach, we assigned individuals to the treatment and control groups based on the characteristics of their ‘main job’ in February.[55] There is not enough information in the LLFS on an individual's secondary job(s) to discern if those jobs were also worker-eligible for JobKeeper.

Our baseline estimates will understate the effect of JobKeeper worker eligibility on employment if some individuals in our control group were eligible for JobKeeper via their secondary job(s). One way to explore the extent of this bias is to re-estimate our models after excluding those who held more than one job prior to JobKeeper. This yields estimates of the effect of JobKeeper worker eligibility on employment that are 0.9 to 1.9 percentage points (or 10 to 20 per cent) larger than our baseline estimates during April to July. While this may suggest that some multiple-job holders in our control group did receive JobKeeper (and so our baseline estimates are biased downward), it may also reflect that multiple-job holders were less likely to have exited employment in the absence of JobKeeper.[56] In the LFS, a person remains ‘employed’ if they hold onto at least one of their jobs; all else being equal (and assuming that job losses are independent events), this is more likely to occur if a person had more jobs to begin with.[57] In other words, the treatment effect of JobKeeper on employment is plausibly smaller for multiple-job holders than for single-job holders because the former group were more likely to retain at least one job in the absence of JobKeeper. Again, it is worth reiterating that our analysis focuses on whether JobKeeper preserved employment, not jobs.

## Appendix E: Alternative Identification Strategy

As a sense check on our baseline results, we also estimated the effects of JobKeeper on employment using a different component of the worker-eligibility test – the residency requirement. With the exception of New Zealand citizens, temporary residents were not eligible for JobKeeper.[58] This residency requirement provides us another way of estimating the causal effect of JobKeeper on employment.

## E.1 Treatment and Control Groups

In this alternative approach, we focus entirely on differences in worker eligibility arising from the residency requirement, rather than the job tenure threshold used for our baseline results. As with the baseline approach, we begin by identifying two groups of workers that are similar aside from the fact that one of the groups does not meet the residency requirement and therefore cannot receive JobKeeper (the control group) and the other group does satisfy the residency test (treatment group). By comparing the average employment rates across these two groups before and after JobKeeper we can derive an estimate of the causal effect of JobKeeper on employment. As before, to do this we use person-level data from the LLFS and a difference-in-differences approach.

Specifically, we define the treatment group as workers who held a Subclass 444 (Special Category) Visa, notably citizens of New Zealand. Unlike other temporary visa holders, people on 444 visas are eligible for JobKeeper. The control group is recent arrivals on all other types of temporary visas, who are not eligible for JobKeeper.[59] Note that unlike our baseline approach, the treatment and control groups using the alternative identification strategy include a mix of casual and non-casual employees and self-employed.[60]

As the descriptive statistics in Table E1 show, recent arrivals from New Zealand are similar to recent arrivals from other countries in a number of ways, such as in the types of industries they tend to work in (in most cases). The main difference is that a smaller share of recent migrants from New Zealand were studying in Australia compared to those from other countries (and, as such, migrants from New Zealand also tend to be slightly older than other migrants, on average). We account for the differences in study patterns and age by controlling for these factors (and other factors) in our model directly.

Table E1: Descriptive Statistics for Recent Migrant Sample
Sample means
Control group (non-Oceanic born) Treatment group (born in New Zealand
or other Oceania)
Difference p-value of difference
Industry (%)
Agriculture, forestry & fishing 2.6 0.0 2.6 0.2932
Mining 0.8 7.3 −6.5 0.0003
Manufacturing 7.4 2.4 5.0 0.2306
Electricity, gas, water & waste 1.0 2.4 −1.5 0.3853
Construction 6.1 4.9 1.2 0.7515
Wholesale trade 3.3 9.8 −6.5 0.0340
Retail trade 12.9 7.3 5.5 0.3006
Accomm & food services 12.9 14.6 −1.8 0.7425
Transport, postal & ware 7.4 12.2 −4.8 0.2675
Info media & telecom 1.3 0.0 1.3 0.4603
Finance & insurance 1.8 4.9 −3.1 0.1759
Rental, hiring & real estate 1.3 0.0 1.3 0.4603
Prof, scientific & tech services 12.5 2.4 10.1 0.0536
Admin & support services 5.8 9.8 −4.0 0.2992
Public admin & safety 0.0 0.0 0.0 na
Education & training 4.1 4.9 −0.8 0.8142
Health care & social assistance 13.5 7.3 6.2 0.2564
Arts & recreation 1.3 2.4 −1.1 0.5535
Other services 4.0 7.3 −3.4 0.2977
Employment type (%)
Casual 33.4 36.6 −3.1 0.6808
Permanent 55.4 63.4 −8.1 0.3152
Other 11.2 0.0 11.2 0.0235
Job tenure (years) 1.8 1.9 −0.1 0.7446
Occupational skill level 3.1 2.9 0.2 0.4928
(1 = highest, 5 = lowest)
Hours worked 31.3 33.7 −2.4 0.3080
One job only (%) 93.4 97.6 −4.2 0.2914
Student (%) 24.5 12.2 12.4 0.0723
Age (years) 32.7 35.7 −3.0 0.0216
Female (%) 42.7 53.7 −11.0 0.1699
Observations 607 41

Note: Characteristics in February for sample remaining in June 2020; employees and self-employed who arrived in the past 1–6 years

Sources: ABS; Authors' calculations

During the GFC, the rate of unemployment experienced by recent arrivals from New Zealand and the unemployment rate experienced by recent arrivals from other countries increased by a similar amount, suggesting these groups have similar sensitivity to changing economic conditions (Figure E1). This gives further confidence that labour market outcomes of these two groups would also have tracked quite closely during the COVID-19 period in the absence of JobKeeper. In contrast, Australian-born workers' outcomes are less sensitive to economic conditions, so using Australian-born as the treatment group would likely lead us to overstate the effects of JobKeeper on employment.

## E.2 Inferring Visa Status and Type

The LFS does not ask people whether they hold a visa or the type of visa they hold. But it does collect enough information to infer the likelihood a person holds a particular type of visa, if at all.[61] This includes:

1. Years since arrival

Survey and administrative data sources suggest that the longer a person lives in Australia, the more likely they are to be a citizen or permanent resident rather than a temporary resident (Figure E2).[62] This reflects the progression of temporary residents to permanent residency over time, and that those who do not attain permanent residency are more likely to leave the country.

We limit our estimation sample to migrants who arrived within the past 1–6 years (measured as of February 2020). The administrative data suggest that roughly half of all people who migrated to Australia within the past six years (and continue to live in Australia) are on a temporary visa, while the other half have attained permanent residency or citizenship (Figure E2). This means that our regression estimates – which pool over all people who arrived within the past 1–6 years regardless of their residency status – will underestimate the effect of JobKeeper by about one-half, all else being equal. We adjust for this bias by applying a scaling factor to our regression estimates (see Section E.4 below).

Our decision to focus on people who arrived in the past 1–6 years is designed to balance the trade-off between ensuring a large enough sample to estimate our regression coefficients precisely and diluting the share of the sample that actually hold a temporary visa.[63] We exclude those who arrived in the past 12 months because labour market outcomes of this group are volatile and unrepresentative.

1. Country of birth

To infer the type of visa a person holds, we use their country of birth as a proxy. Administrative data indicate that virtually all temporary residents born in New Zealand hold a 444 visa (ABS 2019a). The same is true for those born in other Oceanic countries, such as Samoa, the Cook Islands and Fiji, where 85 per cent of all temporary residents in Australia are on 444 visas (meaning they had New Zealand citizenship before migrating). In comparison, less than 10 per cent of temporary residents born outside the Oceanic region hold a 444 visa.[64]

We allocate migrants who arrived in the past 1–6 years to the treatment group if they were born in New Zealand or other Oceanic country, and to the control group if they were born elsewhere. Our estimation sample is restricted to those employed in February 2020, which means we implicitly focus on those with work rights.[65] We apply a (additional) scaling factor to our difference-in-differences estimates to account for the imperfect overlap between country of birth and whether a person holds a 444 visa or not (see Section E.4 below).

## E.3 Estimation Equation

To estimate the effects of JobKeeper residency eligibility on employment we estimate a model similar to Equation (2), but replacing Eligi with a dummy variable that equals one if the worker was born in New Zealand or other Oceanic country, and zero if they were born elsewhere. We also include all the variables listed in Table E1 as controls (all of which are measured as of February 2020). We estimate this equation month-by-month using a linear probability model with robust standard errors.

## E.4 Results

The top panel of Figure E3 shows the share of the treatment (dark line) and control group (light line) that were employed in each month between November 2019 and July 2020, conditional on being employed in February. Around 90¾ per cent of recently-arrived New Zealanders who were employed in February 2020 were still employed three months later, compared to 81½ per cent of those recent arrivals born in other countries. The difference in these employment rates in May – 9½ percentage points – is our difference-in-differences estimate for that month. These estimates are presented in the bottom panel of Figure E3, along with 95 per cent confidence intervals.

As discussed above, we need to apply a scaling factor to these regression estimates to account for the differences between the variables we observe in the data – country of birth and years since arrival – and what we would ideally observe – visa status and visa type. Applying this scaling factor (2.17) to our difference-in-differences estimates suggests that being worker-eligible for JobKeeper raised a person's probability of remaining employed by around 20 percentage points in May and 27 percentage points in June.[66] This is more than twice as large as the intent-to-treat effect we estimated using our baseline approach. The estimates for July were smaller and not statistically significant.

The implied effect of actually receiving JobKeeper on employment is also larger than our baseline estimate. To see this, we again assume that one-third of all worker-eligible individuals received JobKeeper.[67] This suggests that receiving JobKeeper increased a person's probability of staying employed by more than 60 percentage points in May and June, relative to the counterfactual of not receiving JobKeeper. This is three times larger than our baseline estimate. One possible explanation is that the effects of JobKeeper are heterogeneous, with JobKeeper being more effective at preserving employee-employer relationships within the population of recently arrived migrants than it was at preserving those relationships amongst permanent residents and citizens. However, the confidence intervals around this estimate are large (and likely larger than indicated on Figure 3).

It is reassuring that both identification strategies lead to the same overall conclusion that JobKeeper played a key role in cushioning employment losses in its first four months. In both cases, the point estimates are economically and statistically significant, they just differ in magnitude.

Although the migration approach provides a useful sense check, our overall assessment about the quantitative effect of JobKeeper on total employment is based on our preferred approach using the tenure eligibility of casuals. We have more confidence in the results from our baseline approach, as it has fewer potential issues than the migration approach (discussed below). If we had placed more weight on the migration approach, our headline estimate of the employment effect of JobKeeper would be larger.

## E.5 Limitations

Relative to our baseline approach (using the 12-month tenure rule for casual workers), the alternative identification strategy has several shortcomings that explain why we give it less emphasis:

1. Sample size: there are only 53 individuals in the treatment group (801 in the control group) for estimating the employment effect in May.[68] There is a risk that our IV-style estimator suffers from a small sample bias.
2. Adjustments for incomplete data: imperfect measures of visa status and visa type mean we need to make adjustments to our regression estimates that can introduce error. Also, the standard errors do not account for these adjustments, so the precision of our estimates is likely overstated.
3. Parallel trends: the treatment and control groups are far less balanced on observable dimensions than in the baseline approach (Table E1). Although we control for these variables in our model, this lack of balance on observables suggests a greater risk that the treatment and control groups will also differ in terms of unobservable factors associated with employment loss. Indeed, there is some evidence of an ‘effect’ of JobKeeper before the program was announced (Figure E3, albeit not statistically significant), which may signal a violation of the parallel trends assumption.
4. External validity: recent migrants are likely less representative of the broader population of JobKeeper recipients than the casual sample used for the baseline results. For example, most recent migrants do not have access its other forms of income support, such as the JobSeeker payment, which could influence their responses.
5. Selection bias: our estimates may be biased if temporary visa holders departed Australia (and thus drop out of our sample) if their work prospects were adversely affected by COVID-19.[69] The number of visa holders from New Zealand remained fairly steady during the COVID-19 crisis, while those from all other countries have fallen sharply (Figure E4).

## E.6 Differential Treatment Effects by Employment Type

Although our main approach is restricted to casual employees, the migration approach captures the effects of JobKeeper on both casual and permanent staff, and also the self-employed. The estimates in Figure E3 restrict the effects of JobKeeper worker eligibility to be constant across these different categories of employment. Relaxing this assumption allows us to test whether the effects of JobKeeper worker eligibility differs for casuals and permanent employees.[70]

To investigate this further we augment our model with an interaction between the treatment variable and a dummy variable that equals one if the worker is a permanent employee, and zero otherwise.[71] A test for differential effects for employees on different work arrangements is a test of whether the coefficient on this interaction is statistically significant. The coefficient is close to zero and not significant (p-value = 0.66, 0.64 and 0.31 in May, June and July). That is, we cannot reject the hypothesis that the effects of JobKeeper on casuals and permanent employment are equal. We discussed this finding in Section 8.3. An issue with this test is that it is based on a very small sample (particularly at the subgroup level), so has low power.

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## HILDA Survey Disclaimer

This paper uses unit record data from the Household, Income and Labour Dynamics in Australia (HILDA) Survey. The unit record data from the HILDA Survey was obtained from the Australian Data Archive, which is hosted by The Australian National University. The HILDA Survey was initiated and is funded by the Australian Government Department of Social Services (DSS) and is managed by the Melbourne Institute of Applied Economic and Social Research (Melbourne Institute). The findings and views based on the data, however, are those of the authors and should not be attributed to the Australian Government, DSS, the Melbourne Institute, the Australian Data Archive or The Australian National University and none of those entities bear any responsibility for the analysis or interpretation of the unit record data from the HILDA Survey provided by the authors.

## Acknowledgements

For helpful comments and suggestions we thank Natasha Cassidy, Iris Chan, Nathan Deutscher, Pauline Grosjean, Jonathan Hambur, Gabrielle Penrose, John Simon, Lachlan Vass, Luke Willard and seminar participants at the Reserve Bank of Australia and Australian Treasury. We would like to thank the Australian Bureau of Statistics for making the LFS microdata data available to us, and in particular to Scott Marley for his assistance. The views expressed in this paper are those of the authors and do not necessarily reflect the views of the Reserve Bank of Australia. The authors are solely responsible for any errors. Our programs and publicly available data are available at <https://www.rba.gov.au/publications/rdp/2020/2020-07/supplementary-information.html>.

## Footnotes

The 3.5 million figure is based on Treasury's (2020b) estimate for May 2020 and more recent reports in the Budget (Australian Government 2020a, p 1-13) (these are point-in-time figures). The budget papers also noted that more than 3.8 million people have received the JobKeeper payment at some point since the program's inception. [1]

This amount is close to the national minimum wage for full-time employees (\$1,481.60 per fortnight). [2]

The first of these ATO payments to eligible firms were made in arrears in the first week of May, and then on a monthly cycle thereafter. [3]

The New Zealand wage subsidy scheme has different payment rates for full-time and part-time workers. Cassells and Duncan (2020) emphasise the uniqueness of the flat payment rate. The authors note that ‘[o]f the more than fifty countries that have introduced emergency wage subsidies over the course of the pandemic, none paid a single rate to all eligible workers regardless of their normal wage or employment status’ (p 109). [4]

Hamilton (2020) argues that the flat per-worker subsidy undercompensates businesses for their higher earners, and the wage floor prevents them from being overcompensated for their lower earners. Cassells and Duncan (2020) note that most international wage subsidy schemes impose a floor on the amount an employer must pay an employee, normally a fraction (below 1) of the employee's usual wage. [5]

Revenue is on a consolidated basis, so includes the revenue of any individual or business affiliated with the entity. Self-employed individuals were eligible to receive the JobKeeper Payment where they met the relevant turnover test. There were also some additional restrictions on eligibility; for example, public sector agencies and entities subject to the Major Bank Levy were ineligible (ATO 2020a). [6]

On 7 August 2020, it was announced that from 3 August 2020 the relevant date of employment for assessing eligibility would move from 1 March to 1 July 2020, expanding employee eligibility for the existing scheme and the extension. [7]

An ABS (2020a) survey in late April revealed that 90 per cent of eligible firms (with at least some eligible employees) had enrolled in the program or were intending to do so. The reasons firms cited for not enrolling included insufficient cash flow to continue paying workers until the JobKeeper payments commence (23 per cent), difficulty understanding the eligibility criteria (23 per cent) and ‘other’ reasons (54 per cent). [8]

An employer could dismiss an employee receiving JobKeeper by following the usual process for ending employment (FWO 2020b). [9]

Data from ABS (2019a) and the 2016 Australian Census indicated that temporary residents accounted for around 18 per cent of total employment in the accommodation & food services industry in 2016, which was the highest employment share of any industry. [10]

The PPP extends forgivable loans to small businesses, via private banks. The forgiveness is achieved by maintaining employment at pre-COVID-19 levels, which means PPP loans constitute an implicit wage subsidy (Hamilton 2020). [11]

There are exceptions, such as Canada's scheme. [12]

Casual employment status is inferred based on the reported absence of paid leave entitlements (either paid holiday leave or paid sick leave). According to the ABS (2015), this is ‘the most objective and commonly used measure of casual employment’. [13]

In Appendix D.6, we show that our results are unlikely to be materially affected by our focus on main jobs rather than both main and second jobs. [14]

If a person did not pass the worker-eligibility test in their main job, they may still have passed in a second job. We discuss this in Appendix D.6, along with the results of a robustness test that suggests this does not create a material bias. [15]

Some people who were JobKeeper worker-eligible in their main job may not have received the JobKeeper payment for that job if they instead received the payment for a job that was not their main job. But, in that case, the person still received JobKeeper. The individual's main job (as defined in the LFS) can differ from their primary employer (as defined by the ATO). [16]

Table C1 compares the descriptive statistics in Table 1 with equivalent descriptive statistics for the sample of all casual employees in February 2020 (including those with less than 6 months of tenure or more than 23 months of tenure) and the sample of all employees in February 2020 (including all casual and non-casual employees). [17]

An alternative approach would be to control for these pre-treatment differences directly (interacted with the time dummy). However, introducing control variables will only account for observable differences between the treatment and control groups, not the unobservable differences that may have affected employment outcomes in the absence of JobKeeper. [18]

In Appendix D.4, we present evidence that an employee's job tenure as at February 2020 was not predictive of his or her probability of remaining employed over the May to July period, for those people with 1 to 10 months tenure. This suggests that our baseline results would be robust to varying the width of the tenure window on the left-hand side of the 12-month cut-off. [19]

Some key awards that include this provision include the Hospitality Industry (General) Award [MA000009], Fast Food Industry Award [MA000003], General Retail Industry Award [MA000004], Hair and Beauty Industry Award [MA000005] and the Real Estate Industry Award [MA000106]. What constitutes ‘reasonable grounds’ to refuse the request varies by award, but can include: the employee does not work regular hours, the employee's job will not exist in the next 12 months, or the employee's working hours will be significantly reduced in the next 12 months. In other awards, a casual conversion request can be made after 6 months, such as the Manufacturing and Associated Industries and Occupations Award [MA000010] and the Building and Construction General On-site Award [MA000020]. [20]

The 12-month threshold for requesting flexible work arrangements, unpaid parental leave or permanent employment is not anchored at a fixed point in time (unlike the threshold for JobKeeper eligibility which was anchored at 1 March), which means that some of the lower-tenure group became eligible for these options during the April to July 2020 period. [21]

The key identifying assumptions of RDD are likely to be satisfied in that there was very limited scope for employers to manipulate the job tenure information given to authorities (see Section 2.3). Using these other datasets it may also be possible to exploit discontinuities in the revenue decline cut-offs in the firm-eligibility test. In saying that, the revenue decline cut-offs were fuzzier than the cut-offs that applied to individual workers, particularly given that firm eligibility could be based on projected, rather than actual, revenue losses, and that alternative tests could also apply. [22]

The LLFS micro data does not include a variable for whether the employee works in the public sector, so instead we drop employees in 3-digit industries where more than 60 per cent of employees are employed in the public sector (based on data from the 2016 Census). In addition to all industry sub-groups within the Public Administration & Safety industry division, this includes employees working in hospitals, tertiary education, rail and some utilities. The LLFS micro data does not identify whether the employee works for a major bank, so we drop any employees who works in the 3-digit Depository Financial Intermediation industry. Industry in the LLFS pertains to the individual's main job. [23]

By June, there were 377 people in the treatment group and 274 people in the control group. By July, there were 273 in the treatment group and 189 in the control group. More than two-thirds of people in February 2020 had left the panel by July. Much of this sample loss reflects the 8-month rotating panel design of the LFS, which reduces the initial sample by roughly one-eighth for every month we extend our analysis into the future. By July, sample rotation accounts for over 90 per cent of all exits from the survey panel relative to February, while premature attrition (attrition not explained by rotation) accounts for the remainder. While sample rotation leads to some data being ‘missing at random’, a potential source of bias in our study is the possibility that premature attrition does not occur at random. While our treatment and control groups are balanced across many of the observable dimensions that tend to be associated with attrition (e.g. age, occupational skill level), it is possible that premature attrition is also correlated with changes in a person's employment status, and if so, it can create a bias in our regression estimates. One source of premature attrition happens when households change their address, because the ABS drops those households from the survey. Because regional mobility is often associated with a change in employment status (e.g. a person who loses their job may relocate to a new region to find work), this non-random premature attrition could lead to a bias in our estimates. However, during COVID-19 this ‘mobility bias’ is likely to be smaller than normal, due to the constraints on moving home during the pandemic. In July, the premature attrition rates were higher for our control group (8.2 per cent of the February control group sample) than for our treatment group (5.7 per cent of the February treatment group sample). As such, if we assume those who prematurely left the panel did so as a result of job loss, our estimates of the effect of JobKeeper on employment would be understated. Indeed, if all the people who prematurely left the survey panel did so because of job loss, adjusting our difference-in-differences estimates to account for this (by setting the employment status of all premature leavers to ‘non-employed’ rather than ‘missing’) would yield estimates of the effect of JobKeeper worker eligibility on employment equal to 12.9 percentage points, which is higher than our baseline estimate of 8.2 percentage points (Figure 2). The bias will run in the opposite direction if premature attrition is negatively associated with employment. [24]

These changes were announced on 7 August 2020 and effective from 3 August. The August LFS referenced the period 1–15 August. [25]

A person who is not employed can either be unemployed or not in the labour force. We do not distinguish these states. [26]

We are being loose with our terminology here. Our difference-in-differences estimate actually yields the effect of JobKeeper tenure eligibility. This is slightly different to the effect of worker eligibility because the latter also requires the worker meet the residency requirement. [27]

Clustering the standard errors at the 2-digit ANZSIC 2006 industry level (at least 52 clusters over May to July 2020) produced standard errors that were 26 per cent (May), 18 per cent (June) and 6 per cent (July) smaller than robust standard errors that do not allow for intra-industry correlation. As such, our decision to use robust, rather than cluster-robust, standard errors is conservative. [28]

This is consistent with the long-standing concepts and practices used in the LFS. For more information, see ABS (2020d). [29]

The ABS payroll data suggest that the number of secondary jobs fell sharply relative to main jobs during our period of analysis (ABS 2020c). In Appendix D.6, we provide some discussion on the effects of multiple job holding on our results. [30]

Table C2 provides the month-by-month regression estimates of Equation (2) in table format. [31]

This lag occurs for two reasons. First, the survey asks about a given reference week. A worker who loses their job midway through that week is classified as employed if they worked at least one hour at the start of the week. This is important for interpreting the April survey, because a number of high-frequency data sources suggest a large amount of job shedding occurred during the reference weeks of the April LFS. There is also evidence for this in the sharp rise in the number of people reporting fewer than their usual hours during the April reference week(s) because they ‘lost or left a job’ during that week. These job losses did not flow through to employment until May. Second, people who are stood down without pay continued to be classified as employed for at least four weeks after being stood down (see Section 5.5). While this treatment of unpaid stand downs is consistent with the best-practice guidelines set out by the International Labour Organization, it differs to the treatment in Canada and the United States where such layoffs lead to an immediate decline in employment. [32]

Future work using administrative data should seek to better understand the relationship between eligibility and take-up across different employment types (e.g. casual or non-casual) and different ranges of job tenure. [33]

See the business case study on page 28 of Treasury (2020b). [34]

Another consideration is the effects of cross-subsidisation coming from infra-marginal employees at the firm who received JobKeeper (e.g. eligible casual employees at the firm with more than two years of job tenure or eligible permanent employees). However, there is no clear reason to believe that this cross-subsidisation effect should be any larger for our control group than for our treatment group. [35]

When thinking about the substitution effect of the JobKeeper Payment program, we abstract from the income effect of the JobKeeper Payment program itself but not the adverse shock to firm incomes caused by the COVID-19 crisis. [36]

The latter group comprises those who have been stood down for more than four weeks without pay. [37]

Treasury (2020b) analysis of business micro data suggests that in the fortnight ending 24 May 400,000 people were stood down on JobKeeper, or around 11½ per cent of all recipients. This is consistent with our analysis of the LLFS micro data, which suggests that in May around 310,000 people were classified as ‘away from work’ for more than four weeks but still being paid by their employer. The small discrepancy between the Treasury's estimate and our own estimate based on the LLFS may reflect that our estimate excludes any stood down JobKeeper recipients who also held a second job or who found work at another firm. [38]

If the effect of JobKeeper worker eligibility on employment and total hours is 7 per cent and 5 per cent respectively, the effect on average hours worked is approximately –2 per cent. [39]

The confidence intervals in Figure 1 reflect the confidence intervals on our estimates of the effect of worker eligibility and do not account for the uncertainty related to our estimate of the take-up rate discussed in Section 6.2. [40]

Treasury estimated the unemployment rate would peak at 10 per cent with JobKeeper and 15 per cent without JobKeeper (Frydenberg 2020). This ex ante estimate was not affected by the revelation of a reporting error in estimates of the number of employees likely to access the program (and associated budget costing revisions) announced in May (Treasury and ATO 2020). [41]

The implied amount of employment saved by Treasury's estimate will be larger than 700,000 if some of those who exit employment are assumed to leave the labour force rather than becoming unemployed. [42]

The PPP funds could fully cover a firm's pre-COVID payroll expenses for 10 weeks, or one-quarter of their pre-COVID payroll expenses for 24 weeks (or anywhere in between). [43]

In most awards, casual employees are required to be paid an hourly wage premium, which helps to at least partly compensate for the loss of other benefits. [44]

The choice of employment relationship is also endogenous to the value of the worker-firm match. Casual and permanent employees may also have different levels of productivity, firm-specific human capital and wages. [45]

Data from the HILDA Survey suggests that 83 per cent of casuals with at least 12 months of job tenure who were working in the industries most adversely affected by COVID-19 (namely store-based retailing excluding food & fuel, arts & recreation, accommodation & food services, and other services) would have had their pre-scheme earnings more than fully covered by JobKeeper (i.e. a replacement ratio equal to 1 or more), compared to only 31 per cent of non-casual employees. This calculation assumes all employees received wage increases of 3 per cent per year between late 2017 and late 2019. [46]

For a discussion of the role of workplace-level flexibility in how the labour market adjusts to shocks, see Bishop et al (2016). [47]

In this simplified model, the revenue measure excludes any revenue from the JobKeeper subsidy itself. There are likely other worker- and firm-level variables we need to control for in Model (B1) to get an unbiased estimate of $\tau$ , but for expositional simplicity we assume that all relevant confounders are captured by the $\text{Δ}$Revenuei,f,j variable. [48]

We do not adjust for visa status because we did not exclude temporary visa holders from the estimation sample for Equation (2). [49]

The notion that the numerator and denominator of Equation (B3) do not need to come from the same sample is based on the two-sample IV (TSIV) estimator (see Angrist and Pischke (2009, pp 147–148)). [50]

E(JobKeeperi|Eligi = 1) $={\sum }_{k=1}^{19}\left[\left(\frac{total\text{\hspace{0.17em}}JobKeeper\text{\hspace{0.17em}}recipient{s}_{k}}{no\text{\hspace{0.17em}}of\text{\hspace{0.17em}}workers\text{\hspace{0.17em}}satisfying\text{\hspace{0.17em}}worker\text{\hspace{0.17em}}eligibilit{y}_{k}}\right)×\frac{estimation\text{\hspace{0.17em}}sampl{e}_{k}}{total\text{\hspace{0.17em}}estimation\text{\hspace{0.17em}}sampl{e}_{k}}\right]$, where k denotes 1-digit ANZSIC 2006 industry division. The number of JobKeeper recipients by industry is from Treasury (2020b, p 43), which we adjust (proportionally) so that industry totals sum to 3.5 million. [51]

Our IV approach yields a local average treatment effect (LATE) – that is, the effect of JobKeeper on employment for those whose treatment status (receiving JobKeeper) is affected by worker eligibility. Always-takers do not exist in our set-up because a worker could not receive JobKeeper if they were not worker-eligible. For this reason, the LATE also corresponds to the ATT (Angrist and Pischke 2009, p 160). [52]

The p-values on the tenure coefficient in May, June and July are 0.14, 0.86 and 0.62, respectively. [53]

After one year, the employee is entitled to four weeks of pay at their base pay rate in the event of being made redundant. The generosity of these redundancy payments increases with every additional year of service up to ten years (FWO 2020c). [54]

In the LFS, an individual's main job is the job in which they usually work the most hours. [55]

Part of the difference might also reflect that multiple-job holders in our treatment group were more likely to receive JobKeeper than single-job holders in our treatment group, to the extent that they were also worker-eligible in their secondary jobs. [56]

Our analysis of ABS data for 2016/17 (ABS 2019b) suggests that two-thirds of multiple job holders who worked in one of the industries that were most adversely affected by COVID-19 (i.e. hospitality, arts, retail, real estate or other services) were partly ‘insured’ against the shock as they also held a second job in one of the less-affected industries. [57]

To be eligible for JobKeeper, a person must have been an Australian citizen or have held a permanent visa or Special Category (Subclass 444) Visa (and were a resident for Australian tax purposes) as at 1 March 2020 (Treasury 2020a). [58]

As at 30 March, there were 965,000 temporary visa holders with a right to work in Australia (excluding New Zealand citizens), of which 59 per cent were students. The remainder of those with work rights held a working holiday maker, temporary skilled, or temporary graduate visa. These data are from the Department of Home Affairs (2018). Not all visa holders with a work right will exercise that right, especially partners and children of a primary visa holder. These figures include secondary visa holders (i.e. family members), who typically also have work rights. Temporary visa holders with a work right are entitled to the same basic rights and protections as Australian citizens and permanent residents under Australian workplace laws (Migrant Workers' Taskforce 2019). Student visa holders are limited to working a maximum of 40 hours per fortnight during teaching periods, and unlimited hours during vacation periods. [59]

We exclude from the sample any worker employed in the public sector or for a major bank. [60]

The LFS only collects data on usual residents of Australia, which means the survey excludes overseas visitors. The official ABS definition of a usual resident is a person who has been (or expects to be) residing in Australia for 12 months or more in a 16-month period. However, the LFS uses a less precise approach; a screening question simply asks if the respondent is a short-term resident and, if so, they are excluded from the survey (ABS 2017). This criterion is based on a person's duration of stay within Australia. [61]

There are differences in the scope of these collections. The Census excludes those who indicated they would be usually resident in Australia for less than one year (‘overseas visitors’). [62]

Unlike other temporary migrants, New Zealand citizens who have lived in Australia for at least 10 years without interruption are eligible for JobSeeker for up to 6 months. Excluding people who have resided in Australia for more than 10 years means we will not accidentally attribute the effects of some other policy (e.g. JobSeeker) to JobKeeper. [63]

The share of temporary residents on 444 visas is relatively high for those born in the United Kingdom (28 per cent) and South Africa (54 per cent). [64]

Clearly some people in Australia without work rights may still seek work in the underground economy. However, after accounting for the screening questions in the LFS, it is unlikely that migrants working illegally represent a material share of our estimation sample. [65]

This scaling factor is calibrated using data from external administrative and survey sources. It accounts for the share of recent arrivals that are temporary, rather than permanent (around 52 per cent) and also a small adjustment for the fact that a small share of the control group also hold a 444 visa (around 6 per cent). This implies that 46 per cent of our control group is likely to be definitely ineligible for JobKeeper based on their residency status. In turn, this means we need to scale our resulting difference-in-differences estimate by 2.17 (= 1 ÷ 0.46) in order to get an intent-to-treat effect that is consistent with the intent-to-treat effect estimated using the baseline approach. This scaling factor is different to the scaling factor needed to translate our estimates of the effect of worker eligibility to estimates of the effect of JobKeeper. [66]

The take-up rate is close to ⅓ when we stratify the take-up rate calculation by the industry composition of the recent migrant sample. [67]

In June there are 41 and 607 individuals in the treatment and control groups, respectively, and 31 and 423 in July. [68]

Even if our treatment and control groups had experienced similar COVID-19 shocks overall, this non-random attrition from the sample would lead us to understate the effects of JobKeeper on employment amongst those who remained in the sample. However, to the extent that this fall was driven by border closures preventing re-entry of foreigners, rather than because of increased exits due to labour market conditions, this attrition need not be a source of bias. Our sample is matched, meaning that students who did not return to Australia for study in early 2020 are not included anyway. [69]

Casual and permanent employees may also have different levels of productivity, firm-specific human capital and wages. [70]

The base category is casual employees. We also include interactions for ‘other’ employment types (self-employed and contributing family workers) and the main effects. [71]