WPS7924
Policy Research Working Paper 7924
Labor Drops
Experimental Evidence on the Return to Additional
Labor in Microenterprises
Suresh de Mel
David McKenzie
Christopher Woodruff
Development Research Group
Finance and Private Sector Development Team
December 2016
Policy Research Working Paper 7924
Abstract
The majority of enterprises in many developing countries lasting impact on employment, profitability, or sales. Two
have no paid workers. This paper reports on a field experi- supplementary interventions and treatment heterogeneity
ment conducted in Sri Lanka that provided wage subsidies suggest the lack of impact is not due to complementari-
to randomly chosen microenterprises to test whether ties with capital or management skills, and detailed survey
hiring additional labor would benefit such firms. In the data help rule out a number of theoretical mechanisms
presence of labor market frictions, a short-term subsidy that could result in sub-optimally low employment.
could have a lasting impact on firm employment. Using The study concludes that the urban labor market facing
12 rounds of surveys to track dynamics four years after microenterprises does not have large frictions that would
the end of the subsidy, the study finds that firms increased prevent own-account workers from becoming employers.
employment during the subsidy period, but there was no
This paper is a product of the Finance and Private Sector Development Team, Development Research Group. It is part of
a larger effort by the World Bank to provide open access to its research and make a contribution to development policy
discussions around the world. Policy Research Working Papers are also posted on the Web at http://econ.worldbank.org.
The authors may be contacted at dmckenzie@worldbank.org.
The Policy Research Working Paper Series disseminates the findings of work in progress to encourage the exchange of ideas about development
issues. An objective of the series is to get the findings out quickly, even if the presentations are less than fully polished. The papers carry the
names of the authors and should be cited accordingly. The findings, interpretations, and conclusions expressed in this paper are entirely those
of the authors. They do not necessarily represent the views of the International Bank for Reconstruction and Development/World Bank and
its affiliated organizations, or those of the Executive Directors of the World Bank or the governments they represent.
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Labor Drops:
Experimental Evidence on the Return to Additional Labor in Microenterprises#
Suresh de Mel, University of Peradeniya
David McKenzie, World Bank
Christopher Woodruff, University of Oxford
JEL Classification codes: O12, O17, D22, J46, L26, C93
Keywords: microenterprise, labor market frictions, field experiment.
#
Funding for this project was provided by the National Science Foundation (SES0820375), the World Bank, DfID,
the Knowledge for Change Trust Fund, the Diagnostic Facility for Shared Growth Trust Fund, the Strategic Research
Program Trust Fund, and the Templeton Foundation. Matthew Groh provided excellent research assistance. The
surveys and interventions were carried out with aplomb by the Kandy Consulting Group, without whose assistance
we would not have been able to undertake the project.
1. Introduction
The modal firm in most developing countries consists of a self-employed entrepreneur with no
paid employees. Do labor market frictions prevent more of these firm-owners from hiring workers?
The development literature has long characterized rural labor markets as incomplete, leading to
non-separation of household production and consumption decisions (Rosenzweig, 1988 provides
a review). But there is theoretical debate as to the extent to which there are frictions in urban
markets. A long-held view has been that of dualism, in which large, formal firms face serious
frictions from minimum wages and other regulations, but smaller firms operate without frictions
in an unregulated sector (e.g. Fields 1975; Rauch 1991; Zenou 2008).
However, more recent literature argues that minimum wages and other regulations can have
spillovers that distort the informal sector (Freeman, 2010). Moreover, even in the absence of
regulatory distortions, there can be other important frictions. For example, training costs coupled
with high worker turnover may imply that new workers should pay to work at firms for some initial
period, something limited contracting options (Stiglitz, 1974) usually rule out.1 Other frictions
arise from imperfect information. The diversity of technologies and products in urban markets may
make it harder to identify the right match for a job (Rosenzweig, 1988); supervision and search
costs may make it prohibitive for firms to expand labor beyond family members (Emran et al,
2008); and owners may lack information even about their own entrepreneurial ability (Jovanovic,
1982).
We conduct an experiment to test directly whether hiring additional labor can benefit small firms
in Sri Lanka. Previous work providing “capital drops” to microenterprises in Sri Lanka found
evidence of capital constraints, but also found that capital alone was not enough to transition firms
to hiring workers (de Mel et al, 2008, 2012). In this paper, we report on an attempt to drop labor
into firms by offering microenterprises temporary wage subsidies equivalent to roughly half the
wage of an unskilled worker for a period of six months. In the absence of frictions, a short-term
subsidy should increase employment during the subsidy period, but have no lasting impact,
1
Apprenticeships common in certain labor markets appear to reflect the low initial marginal product of labor. But
as Hardy and McCasland (2015) show, the efficiency of the apprenticeship solution is compromised by credit
constraints and information frictions.
2
whereas under the alternative labor market models, a temporary subsidy can have long-term
impacts on firm size.
We find that 24 percent of firms take the subsidy to hire a worker, resulting in an increase in
employment in the treated firms during the subsidy period. However, using 12 rounds of survey
data to track the dynamics of adjustment for four years post-subsidy, we show there is no lasting
effect on employment, firm profitability, or sales. A combination of shedding of workers by treated
firms and additional hiring by control firms completely eliminates the employment gap within two
years. The only long-term effect is that the subsidy appears to have increased survival rates for
firms that initially had low-capital and low profitability.
We use the data generated by the experiment to differentiate between competing views of urban
labor markets for small firms. A combination of detailed survey data and an analysis of
heterogeneous treatment effects yields no evidence that owners are learning more about their
ability to manage workers, and suggests that search is not excessively costly for such firms.
Complementary treatments providing either capital or training show that the lack of long-term
effect does not appear to be due to lack of complementary capital or skills. Instead, the estimated
return to additional labor during the subsidy period appears similar in magnitude to the subsidy
offered, suggesting additional workers bring no more value to the firm than their unsubsidized
labor cost. As such, our results imply that labor markets appear to be functioning reasonably well
for microenterprises, and do not appear to be the constraint to their growth that some theories
might suggest.
This paper contributes to a recent experimental literature on frictions in urban labor markets in
developing countries. Much of this literature focuses on interventions to help particular job-seekers
find jobs, by directly offering the job seekers wage subsidies (Galasso et al., 2004, Groh et al.
2016, Levinsohn et al., 2014); and/or by trying to improve the search and matching process through
transport subsidies and skill certification (Groh et al, 2015; Abel et al, 2016; Abede et al, 2016).
Some, but not all, of these studies have found modest improvements in formal employment as a
result of this assistance, consistent with constraints to workers finding jobs in larger, more formal
firms. These studies have not explicitly focused on helping workers find employment in
microenterprises, and have not typically found significant effects on informal employment.
3
The literature examining labor market frictions from the firm side is much less developed, with
several recent studies beginning after this paper. Cohen (2016) develops a structural model using
data from our earlier capital experiment in Sri Lanka and finds, under specific assumptions, that
microenterprises do seem to be constrained in expanding labor as their capital grows. Bertrand and
Crépon (2016) find that firms with between five and 300 employees in South Africa hire more
workers when offered labor law advice that explains to them that firing restrictions are not as
burdensome as many firms think, suggesting constraints on labor expansion for SMEs. In work
most closely related to ours, Hardy and McCasland (2015) randomly place apprentices with small
firms in Ghana, and find firms retain this extra labor for at least six months, and earn higher profits
in doing so. Their context, in which employees typically pay for entry-level positions in order to
get trained, differs from the standard labor market contractual form in most developing countries
(including Sri Lanka). If their results persist over time, this may explain the difference in results.
The remainder of the paper is structured as follows: Section 2 outlines different theories of why
small firms might be labor constrained, and the implications for the impact of a wage subsidy;
Section 3 details the experimental design and intervention; Section 4 discusses take-up; Section 5
provides the results; Section 6 investigates different mechanisms leading to these results; and
Section 7 concludes.
2. Theory: Why Might Small Firms Be Labor-Constrained, and How Could a
Temporary Subsidy Have Lasting Impacts on Firm Employment?
The most common firm size in many developing countries, including Sri Lanka, is one – an owner
with no paid employees. What explains the small size of these firms, and how might we expect a
temporary wage subsidy to change this firm size?
2.1 Classic complete markets model
Consider first the standard complete markets model of firm size of Lucas (1978), where differences
in employment size among firms facing the same output production technology f(.) reflect
differences in their management ability and productivity, θ. A firm facing a wage rate for workers
w, and an interest rate on capital r, will choose capital, K and labor, L to maximize profits f(θ,K,L)
– wL – rK. Firms are small and are assumed to be price-takers, who can sell all output they produce
at a price normalized to 1. This yields the familiar first-order conditions in which the optimal levels
4
of capital (K*) and of labor (L*) are chosen such that marginal products of labor and capital are
equal to the wage rate and interest rate respectively2:
∗ ∗
, , (1)
∗ ∗
, , (2)
If managerial ability is a complement, rather than a substitute for capital and labor, then in this
model firms with zero workers are those with low managerial ability.
Consider a temporary wage subsidy in this model. This lowers the effective wage rate for
additional workers from w to w’. Resolving the first-order conditions (1) and (2) at this lower wage
will result in firms choosing a higher levels of employment L’, and producing more output, and
therefore more sales and higher profits in the short-run. However, once the subsidy ends, w returns
to its previous level, and – so long as θ is unchanged by the intervention – output, profits, and
employment return to their pre-subsidy levels.
2.2 Standard model with credit constraints
Now consider credit market constraints which limit the ability of firm owners to borrow to finance
capital investments. Let A be the wealth of the business owner. This wealth can be leveraged in
financial markets by some amount (b-1), with b≥1 being a measure of borrowing constraints. The
capital constraint is then K≤bA. Then the new equilibrium levels of capital, K**, and L** solve:
∗∗ ∗∗
, , (3)
∗∗ ∗∗
, , (4)
Where λ is the Lagrange-multiplier on the borrowing constraint. In this set-up, equilibrium output
and equilibrium capital are lower than in the no constraint case (K**<K*), but L** may be greater
than or lower than L* depending on the shape of the production function: firms may substitute
capital for labor and end up with more employment than in unconstrained states, or they may find
labor less productive without complementary capital and so hire less labor than in unconstrained
states.
2
For simplicity of exposition we assume the owner’s own labor supply is inelastic here, but in our empirical
work will also examine the labor supply response of the owner to our interventions.
5
The wage subsidy treatment should then have a similar impact as in the standard model without
constraints, except that the presence of credit constraints may limit the ability of the firm owner to
adjust capital upwards to provide the capital needed for additional labor to work with. This would
act to reduce the responsiveness of firms to a wage subsidy in the short-run. There should again
be no long-run impact.3 An exception to this prediction of no long-run impact may occur if firms
face a lower-bound of profitability below which they shut down if they cannot borrow. The short-
term wage subsidy, by temporarily providing a period of higher profits, may allow the firm to
survive shocks that would otherwise cause them to close down, and thereby remain in business (de
Mel et al, 2012).
2.3 Labor market constraints
The motivation for a wage subsidy instead lies in the idea that there are firms for whom it would
be beneficial to hire more workers, but have not done so due to various constraints on hiring. There
are several possible reasons the labor market may not clear, and why a short-term subsidy may
therefore have a lasting impact.
The first set of frictions are those involved in identifying, hiring, and firing workers in an
environment where firm owners are unsure of worker types. For example, the search and matching
theory of Mortensen and Pissarides (1994) features firms with vacancies who find it difficult to
match with qualified workers. If small firm owners find it hard to identify good workers they can
trust, or find it socially or financially costly to fire them if they are bad, then this cost of hiring will
deter some firm owners from hiring workers who, if they turn out to be good matches, will increase
firm profits. A wage subsidy can subsidize these hiring costs and lead firms to take chances on
new workers. This will increase employment in the short run, and since firms will retain workers
who are good matches, also have a long-term impact on employment.
A related possibility is that firm owners may not know their own type (θ), as in Jovanovic (1982).
Let θ* be the managerial ability cutoff at which the unconstrained optimum is to hire a worker.
Let be the belief a firm owner has about their own ability. If we consider a distribution of initial
3
If the firm is credit constrained and the wage subsidy increases profits in the short run, these profits may be re-
invested, with a resulting long-term effect. But the upper bound on the additional profits in this case is the amount of
the subsidy. In our case, that is 28,000 LKR, while the median (mean) capital stock excluding land and buildings
among the firms in our sample is 160,000 (345,000) LKR.
6
beliefs about own managerial ability, then all owners with initial beliefs ≥ θ* will have tried
hiring a worker before, and either found the worker to be productive and kept the worker, or not
to have been productive and not have kept the worker. The pool of firm owners who have not
previously hired a worker will then consist of owners with low actual managerial ability, as well
as those with high actual managerial ability who believe they have low ability. The wage subsidy
induces some of these owners to take on a worker while the subsidy is in effect. If this enables
them to learn their ability type, then some of these firm owners will discover they were incorrect
in their beliefs and retain the worker after the subsidy ends.
A third set of labor market constraints may arise from the combination of job-specific human
capital and either formal or informal minimum wages that prevent untrained workers being paid
their low marginal product (or even being charged to learn on-the-job as in the apprenticeship
system studied in Hardy and McCasland, 2015). Workers may be less productive in their first few
months while they learn the specifics of the job, with productivity increasing over time through
on-the-job training. For example, one of the firms in our study was a wedding videographer, and
said it took two months of training before a new worker could be sent out to film a small wedding
by himself. In the standard model above, the firm would pay a new worker his or her marginal
product, so would pay a low (perhaps even zero or negative) wage at the beginning, and then a
higher wage once productivity increases. However, poverty constraints, minimum wage laws, and
social norms may limit the ability of workers to take low initial wages to compensate for their low
initial productivity. This imposes the constraint w≥m on the optimization problem, where m is this
lower bound on the wages that can be paid. A short-term subsidy can compensate firms for the low
productivity of workers during this training period, and for the fixed costs of hiring workers. If the
productivity of workers increases during the period wages are subsidized (Bell et al, 1999), then
they may be sufficiently productive after the subsidies end that firms are willing to pay them wage
w≥m and keep them employed.4
A fourth possibility is that of non-convexities in hiring labor: firms may be only able to hire a
worker full-time, or not at all. As a result, some of the firm owners with 0 workers may have
4
Given enough friction in labor markets, firms may be able to recapture initial losses by paying wages
below the marginal product of labor after workers become more productive. But movement of workers
across firms may prevent this.
7
optimal firm sizes of say 0.4 workers. Given the integer constraint, these firms may be more
profitable without a worker than with a worker. The subsidy may change this optimal in the short-
term to be closer to one worker, leading to hiring. The model would predict that, all else equal,
firm owners with higher management ability will be closer to the threshold, and so be more likely
to respond to the intervention. However, since the wage subsidy does not change this non-
convexity, employment afterwards should return back to the original level.
The first three sources of labor market frictions offer the possibility that some firms are small
because of these frictions, and that a short-term subsidy may have lasting impacts on firm size.
However, if labor markets function reasonably well, then we would predict a subsidy to have no
lasting impact on employment. The above theories also offer predictions for which types of firms
may respond more, at least in the short-run, to a subsidy – those with higher management ability
if non-convexities are an issue, younger firms and those with no previous experience with workers
if learning one’s type is an issue, and wealthier firms if credit constraints bind and capital is needed
to make new workers productive.
3 Experimental Design and Data Collection
3.1 The Sample
We aimed to select a random sample of urban microenterprises with two or fewer paid employees,
owned by males aged 20 to 45 and operating in non-agricultural sectors. We chose to focus on
male-owned enterprises because our previous work with capital grants showed that male-owned
businesses appeared to have more growth potential, with female-owned firms facing additional
constraints (de Mel et al. 2008, 2009). We took a random sample of firms, rather than screening
on interest in hiring workers, in order to understand whether the average microenterprise is labor-
constrained.
To attain this sample of firms, we selected Grama Niladhara (GN) divisions within Colombo,
Kandy, and the Galle-Matara areas, and went door-to-door listing households from a random
starting point. The listing collected information on each adult active in the labor force, and was
used to screen on age, self-employment status, and sector to select firms for our sample. This was
then followed by a baseline survey which collected details of the business and the owner. The first
phase of this occurred in April 2008 (see Appendix 1 for a timeline) as part of a larger panel survey
that also included other urban areas in Sri Lanka. We then returned in October 2008 and conducted
8
a booster listing exercise and survey in neighboring GNs in order to attain a larger sample for our
intervention, re-interviewing those interviewed in the original sample. After dropping those firms
that had closed since the first baseline, this gave a sample of 1,533 firms. Appendix 2 provides
more details on the sampling methodology.
3.2 The Intervention
Our main intervention consists of a temporary wage subsidy to firms with the purpose of
encouraging owners to hire an additional full-time employee. The April 2009 survey – taken before
anyone was made aware of the wage incentive program – asked for information about each
employee currently working at the enterprise. In early July, we notified those assigned to the wage
incentive treatment that we would pay a flat amount of 4,000 LKR per month for a period of six
months if they hired an additional employee working at least 30 hours per week, and a flat amount
of 2,000 LKR per month for a further two months. The employee had to be someone living outside
the owner’s household and could not be an immediate family member (spouse, parents, siblings,
and children). Participants were told that payments would start in August 2009 and, regardless of
when the worker was hired, end by May 2010. In other words, workers had to be hired by October
1, 2009, for the full amount of the subsidy to be paid. The subsidy represents about half of the
earnings of a typical unskilled worker. It is also approximately half the minimum wage, which in
Sri Lanka is set by Wage Boards and ranged from approximately 7,000 to 8,000 LKR per month
during the time of the intervention. Note that the minimum wages only apply to formally registered
workers.
Several studies of the impacts of wage subsidies on workers in developing countries have found
employers reluctant to register hired workers formally in the social security system where they
would have to pay labor taxes (e.g. Galasso et al, 2004; Groh et al, 2016). Since the vast majority
of microenterprises in Sri Lanka do not register their workers (de Mel et al, 2013), we did not make
legal registration of workers a requirement of the program. Once we were notified by the
participant that a worker had been hired, we sent a research assistant to conduct an interview with
the new employee. We also conducted a short interview with the owner focused on the search and
hiring process. Research assistants then made occasional unannounced visits to the enterprise to
make sure the employee was working. In a few cases, the research assistants were unable to
confirm that the employee was in fact working full time. In all such cases, within a few visits the
9
owner notified us that the employee was no longer working, and we removed the subsidy. We
believe this process and these spot checks were sufficient to root out minimize ‘phantom’
employees.
In order to determine whether the effectiveness of the wage subsidy differs with the availability of
complementary inputs, we also carried out two supplementary interventions. The first was a
savings intervention, in which individuals were offered a savings account in which we matched
deposits made up to a specified amount. This took place before the wage subsidies started, and the
goal of this intervention was to enable firm owners to build up a balance of savings, which they
could then use to supplement the worker with any additional capital required to make this worker
more productive. The second was a business training intervention, which also took place before
the wage subsidies started. Firm owners were offered the ILO’s Improve Your Business (IYB)
training, to allow for the possibility that better business practices are needed in order to be able to
successfully employ additional labor. Appendix 3 describes these supplementary interventions in
more detail.
3.3 Randomization and Balance
After the baseline survey was conducted with those in the booster sample, we stratified firms into
six strata using geographic region (Colombo, Kandy, or Galle/Matara) and sector (retail or
manufacturing and services). Within each stratum we then randomly assigned 18.7% to the control
group (286/1533), 16.3% (250/1533) to get the wage subsidy program alone, 19.3% (297/1533)
to get the wage subsidy and the supplementary savings program, 19.3% (297/1533) to get the wage
subsidy and the supplementary training program, 7.3% (112/1533) to get the supplementary
savings program alone, 9.2% (141/1533) to get the supplementary training program alone, and
9.8% (150) to get the supplementary training and savings programs.
Given the number of groups and the irregular sample sizes across groups, it was not possible to
stratify further within strata in doing the randomization.5 In order to improve balance further on a
set of key variables likely to be related to business outcomes we therefore employed a re-
randomization procedure. We re-randomized 1,000 times and in each randomization conducted an
F-test for equality of means across the seven treatment groups for a set of 13 baseline variables
5
We chose to put more observations in treatment groups where we were concerned that take-up would be more of
an issue, in order to have sufficient observations in each cell with which to examine intervention take-up.
10
listed in Table 1, including profits, ability, management practices, number of employees, and
business assets. One potential pitfall for this approach can arise from outliers, so we also included
dummy variables for profits and assets in the top or bottom 5 percent to reduce the possibility that
balance on means was disguising large outliers. We then took the maximum F-statistic across these
13 variables, and then choose the random assignment from among the 1,000 allocations that had
the minimum maximum F-statistic. In all reported regressions, we control for the baseline
measures of these variables and for the full set of strata dummies, which Bruhn and McKenzie
(2009) show gives the correct size and power after re-randomizing.
For the majority of this paper we use the sample of 286 pure control enterprises and 250 enterprises
assigned to the wage subsidy treatment alone. Table 1 shows that we achieved balance at baseline
on a set of important observable variables: we are unable to reject the null hypothesis that these
observables are jointly orthogonal to treatment status (p=0.734). In addition, we follow Imbens
and Rubin (2015) in considering the normalized difference / ̅ ̅ /2 as a
measure of balance, where and ̅ are the sample mean and variance of the variable for the
treatment group (j=T) and control group (j=C) respectively. These normalized differences provide
a scale-invariant measure of the difference in locations, and show good balance, with the largest
differences less than 0.2 standard deviations. Appendix 3 also shows balance for the supplementary
interventions.
Table 1 helps provide a descriptive picture of the owners of these firms and their businesses. The
average owner is 35 years old, has finished 10 years of schooling, and works 58 hours a week in
their business. Most firms do not have any paid employees, with only 11 percent having at least
one paid worker, and an average of 0.17 paid workers per firm. The businesses are mostly informal
(only one-third are registered for tax purposes), with 40 percent in retail (e.g. groceries, hardware,
plastic products), and the remainder in manufacturing (e.g. tailoring, brasswork, carpentry, food
production) and services (e.g. electricians, vehicle repair, haircutting, transportation). In 2008,
mean monthly profits were 14,184 LKR (approx. US$130) on 46,434 LKR (approx. US$430) of
monthly sales.6
6
The exchange rate averaged 108 LKR per USD in 2008, was in the 110-115 range from 2009 to 2011, and then
averaged 128 LKR per USD in 2012, 129 in 2013, and 130 in 2014.
11
3.4 Follow-up Surveys and Attrition
After the two rounds of baseline, we conducted six-monthly surveys every April and October from
2009 through 2012, followed by additional surveys in April 2013 and April 2014. Altogether this
provides 12 rounds of data, including 2 to 3 rounds pre-intervention, 2 rounds during the
intervention, and then 7 rounds post-intervention covering four years after the subsidy ended. Each
survey round collected operating data for the previous month, along with details of worker hiring
and other information. Appendix 4 describes in more detail how key variables were measured. For
firms which closed down, we collected information on the current activities of the owner, while
for those who could not be interviewed we attempted to obtain basic information on whether the
business still existed and the number of employees through observation and discussions with
neighbors and family members.
The multiple rounds of follow-up surveys offer several advantages over standard firm studies
which rely on a single follow-up. First, they enable us to trace out the trajectory of impacts, to
determine whether the treatment effects vary over time. Second, by pooling together data from
multiple waves, we can average out seasonality and increase power (McKenzie, 2012). Third, they
give us multiple chances to interview firm owners, since owners who may not be available one
round may be able to be interviewed in a subsequent round. In order to benefit from all three
advantages, we pool together rounds 4 and 5 to capture average effects during the intervention,
rounds 6 and 7 to capture average effects in the first year after the subsidy ended, rounds 8 and 9
to capture average effects in the second year after the subsidy ended, and rounds 10, 11, and 12 to
capture average effects in years 3 and 4 after the subsidy.
Survey attrition was low for a panel of this length with microenterprises. Round by round attrition
rates averaged 5.6 percent for whether the business was in operation, and 9 percent for whether it
had a paid worker (see Appendix 5). Table 2 provides summary information on data availability
by time period and treatment status after we pool together several data rounds as described above.
Data are available for 95 percent of the firms during the intervention period, 95-97 percent in the
first year after the subsidy, 92-99 percent in the second year after the subsidy, and 96-98 percent
in years 3 to 4 post-subsidy. There is no significant difference in attrition rates by treatment status,
except for the second year post-treatment where we have slightly higher data availability for the
control group. The last four columns of Table 1 also show that the sample responding to the last
12
survey round remains balanced in terms of observable baseline differences. Given the lack of
significant differences in attrition by treatment status, and that attrition does not appear to
differentially select firms on observables, we maintain a missing-at-random assumption in our
analysis for those attriting.
An important point of context is that the period of our study coincided with a period of rapid
general economic growth in Sri Lanka. When we began our study in 2008, per-capita GNI (in
constant 2011 PPP international dollars) was 7,598.7 In May 2009, just before our wage subsidy
intervention period began, the 25-year civil war ended, and the Sri Lankan economy grew at 8 to
9 percent per year over the 2010 to 2012 period, with per-capita GNI reaching 10,396 in 2014, the
year of our last survey. We are therefore testing the return to additional labor in a growing
economy, where firms may be expected to have opportunities to potentially grow.
4 Take-up and Who Did They Hire?
4.1 Take-up
During the eight months the incentive program was active, 60 of the 250 firms offered only the
wage subsidy took it up (24 percent). The take-up rates were not statistically different (p=0.622)
in the wage subsidy plus savings (24.2%), and for the wage subsidy plus training (21.2%) treatment
groups, giving a total of 196 firms that used the subsidy for at least one month. Conditional on
using the subsidy, the median firm used it for seven out of the eight possible months and received
a total of 24,000 Rs. in subsidy. Only 17 percent of those using the subsidy used it for 4 or fewer
months, and 68 percent used it for 6 months or more.
Table 3 examines the correlates of the take-up decision, building on early analysis presented in de
Mel et al. (2010) which only had take-up data through to November 2009. We conduct probits of
the probability of using the wage subsidy voucher for the wage subsidy only treatment group, and
for all treatment groups offered the wage subsidy. The first column examines firm characteristics,
the second owner characteristics, and the third both together. We see that take-up rates are lower
in Colombo than in the southern cities of Galle and Matara, with Kandy in between. One possible
reason is that wage rates are higher in Colombo, so the flat-rate wage subsidy may cover a lower
proportion of the worker’s wage there. We find that firm characteristics have very little predictive
7
Source: World Development Indicators, World Bank.
13
power for which firms take up the intervention: there are no significant differences in take-up for
those that already had paid workers, for those firms that were formally registered, for firms that
had more assets at baseline, or by firm age. Instead the skills of the owner appear to matter more.
More highly educated owners, and those employing better business practices at baseline are more
likely to use the subsidy.
4.2 Who did they hire?
In October 2009, we surveyed both the workers hired under the subsidy program and the employers
who hired them. These surveys provide data on the characteristics of the workers and the methods
the owners used to find them. The hired workers are 31.5 years of age and have 9.8 years of
schooling on average. Close relatives of the owners and those living in the owner’s household
were not eligible to be hired, but 31.3 percent of hired workers are related to the owner in some
way; 15.6 percent are female. Most (83.4 percent) were known to the owner before the hiring, and
almost half (48.4 percent) say they live within 1 kilometer of the business. Workers report being
paid 1,860 LKR per week, with just under one-third of them being paid the subsidy amount or
less.8 The excess hiring of relatives is concentrated among lower-profit firms, with 41 percent of
hires by firms with lower than median baseline profits being related, compared with only 20
percent of hires by firms with above median baseline profits (p=0.08). These low profit firms are
also the ones paying the lowest wages: 60 percent of their hires are paid the subsidy amount or
less, compared with only 4 percent of the hires by higher-profit firms (p<.01).
To provide context, we can compare these characteristics with two other groups of hired workers.
The first is workers who were working for control firms in April 2010, and who were hired between
2009 and 2010.9 We have more limited data on these employees, but we find that they are slightly
older (33.6 years of age) and less likely to be female (9.4 percent). They are much less likely to be
related to the owner (9.4 percent) and are paid a higher wage (3,217 LKR per week). A second
8
There is no significant difference in reported hours worked between those paid 1,000 LKR (51.6 hours) per week
or less and those paid more than this amount (52.8).
9
This period encompasses the subsidy period, but is longer so that we have a somewhat larger sample. Among
employees at control firms, 32 were hired in 2009 and 21 in 2010. Note that since this sample is workers employed in
2010, it does not include workers hired but no longer working for the enterprise. We note also that this survey provides
more limited information about the employees, and that wages are reported by employers (rather than employees and
in categories of daily wages, 0-199, 200-399, etc. We estimate average wages from these responses by using the
midpoint of the categorical response, which may over- or under-state the level relative to the continuous response
given in the survey of hired workers.
14
comparison comes from surveys conducted in April 2013 and 2014. From these surveys, we use
data on workers hired by the firms eligible for the subsidies in the three years following the subsidy
period. Compared with the workers hired under the subsidy program, the workers hired later by
the same pool of firms are slightly older (32.6 years) and less likely to be female (10.0 percent),
though neither of these differences is statistically significant. They are much less likely to be
related to the owner (10.0 percent), a difference which is significant at the 1 percent level. They
are also slightly less likely to have known the owner previously (71.4 percent) and to live within
one kilometer of the business (35.7 percent), though these differences are not statistically
significant at conventional levels. They are paid much more (3,350 LKR per week, deflated to fall
2009 prices). On the whole, the characteristics of workers hired post-subsidy are quite similar to
those hired in 2009-10 by the control firms. Hence, it appears that workers hired under the subsidy
are similar except that they are more likely to be related to the owner, and they are paid a lower
wage.
We also asked owners which of 10 methods they used to locate the employee hired through the
subsidy program. Employers relied mostly on networks, with asking friends (50 percent),
neighbors (33 percent), immediate family (21 percent) and extended family (18 percent) for
referrals the most common responses. Advertising the position was very rare, used by only 1
percent of the employers, while contacting former employees (7.7 percent), and contacting friends
(9.3 percent) and relatives (6.7 percent) directly about the job were used with intermediate
frequency. On average, employers used two of the methods. For comparison, in the April 2013
survey, we asked those eligible for the subsidy program how they found employees hired in the
two years after the subsidy period. We find similar patterns though the search intensity is somewhat
higher, with employers using just over 2 methods. With the post-subsidy hires, employers were
more likely to say they advertised (9.6 percent) and contacted former employees (17.2 percent),
but referrals through networks of family, neighbors and friends remain the most common search
methods by very large margins.
5 Results
We first examine whether the wage subsidy changed the survival rates of firms, since, to the extent
it did, we need to control for this in examining impacts on employment, profitability and sales. As
noted above, our estimation aims to combine the advantages of combining multiple follow-up
15
rounds to increase statistical power with also a desire to explore the trajectory of impacts. We
therefore use data for the control group and wage subsidy only treatment group to estimate
treatment regressions using the following specification for outcome Y for firm i in period
t=3,…,12:
, ∗ ∗ ∗ 1 ∗
2 ∗ 3 4 ∑ 1 ′ , (5)
Where Treat is a dummy variable for whether they got the wage subsidy treatment or not; Pre
indicates the pre-treatment, post-baselines round 3, During indicates the two survey rounds 4 and
5 when the wage subsidy was in effect, and Year1, Year2, and Year3to4 indicate the survey rounds
corresponding to 1 year, 2 years, and 3 to 4 years post-intervention; 1 are a set of survey
round time dummies; X is a set of controls for the randomization strata and for the baseline
variables used in randomization (Bruhn and McKenzie, 2009); and the error term , is clustered
at the firm level. The baseline controls include the baseline values of many of our key outcomes
of interest, making this an Ancova specification, but where the baseline value of the outcome of
interest is not in X, we also include it as an additional control when available. Our interest is then
in the trajectory of treatment effects as given by to . To account for multiple testing across
periods we test the equality to test whether the treatment effects are stable, and
0 to test whether we can reject that there is no treatment effect after the
intervention. provides a placebo test, similar to a further balance test, since it uses pre-
intervention data.
Note that the treatment effects we estimate are intent-to-treat effects, which is the impact of being
offered the wage subsidy. This is the relevant parameter for understanding the policy impact of
wage subsidy vouchers. We then turn to estimating the impact of actually hiring an additional
worker in section 5.4.
5.1 Impact on Survival
Table 4 examines the impact of the wage subsidy on firm survival. Businesses temporarily close
and then re-open again, so survival here is defined in terms of whether the owner is self-employed
at the time of the survey round, and includes the case of the owner shutting down one business and
16
starting another one.10 Survival rates are reasonably high in the control group: 95.8 percent of firm
owners are operating their businesses during the intervention period (one year after baseline), 88.8
percent one year after the intervention, and 83.4 percent three to four years later. However, recall
that data on operating status are not available for 3 percent of firms in the three to four-year period,
and these firms may have also closed. We therefore consider two other definitions of survival for
robustness. The first assumes that if a firm is surveyed and found to be closed, and then attrits from
future surveys, that it has remained closed. The second measure makes the assumption that all
attriting firms are closed.
Figure 1 shows graphically the survival pattern round by round, and shows a clear widening of the
gap between the treatment and control groups over time. Table 4 shows that there is no significant
impact on firm survival during the intervention, but significant impacts in all three time periods
afterwards. Those that received the subsidy were 5.8 percentage points more likely to still be self-
employed in our last follow-up rounds. This effect remains significant at the 10 percent level when
we use either of our alternative definitions of survival. We discuss possible reasons for the survival
impact in section 6, after having seen the impacts of the subsidies on employment, profitability
and sales.
5.2 Impact on Employment
To account for this impact on survival, we code firms which are closed as having zero employment,
zero profits, and zero sales in our analysis. This enables us to examine the full unconditional impact
on these outcomes in a way which is not subject to selectivity concerns present in comparing only
firms in operation. We later also provide comparisons of treatment and control profits and sales
conditional on survival.
Figure 2 shows the time pattern of whether firms have any paid workers, and of the average number
of paid workers (truncated at 5 workers, the 99th percentile during the intervention period). We see
the treatment and control groups have similar employment in the baseline and survey pre-
intervention, and that the treatment group hires more workers than the control during the
intervention period. This gap halves in the year following the intervention but is still noticeable,
and then the employment of the two groups looks similar in the last four survey rounds. A further
10
See Appendix 4 for a discussion of alternative approaches to defining survival. All yield qualitatively similar results.
17
point to note is that the control group is slowly growing employment over time, so the
counterfactual is one in which some firms would be hiring even without the subsidy.
The first two panels of Table 5 examine whether this impact is significant. We see during the
subsidy period there is a positive and statistically significant increase in both the likelihood of
having any paid workers, and in the number of workers hired. The 14 percentage point increase in
the likelihood of having any paid workers is relative to a control mean of 27 percent during this
time, so the subsidy has resulted in a 52 percent increase in the likelihood of having a worker
during this period. The impact on the number of paid workers is 0.20 workers, relative to a control
mean of 0.48 workers, so again represents a sizeable increase in relative terms. The impact on
having a paid worker remains positive and significant, at 11.1 percentage points, in the year after
the intervention, but then falls to near zero and is not statistically significant in either the second
or third and fourth years. The impact on the number of paid workers also shows 0.12 workers more
in the year after the intervention, although this gap is not statistically significant, and then falling
further over time to be near zero and not significant in the longer-term.
Figures 3 and 4 delve into the employment changes in more detail by examining the churn in
employment. Figure 3 looks at the probability a firm increases or decreases the number of paid
workers it has between survey rounds. We see treated firms are more likely to be adding workers
during the intervention period, but less likely to be adding workers than the control group between
rounds 7 and 10. Immediately after the intervention the treatment group is more likely to be
reducing the number of workers it has in the six months immediately following the end of the
subsidy. Figure 4 examines how many workers are being changed. We see almost all of the action
is at the margin of a single worker. As the subsidy begins, the treatment group is more likely to be
adding a worker, and once the subsidy ends, it is more likely to be subtracting a worker. We see
that 78 percent of the control group have no change in worker numbers between rounds, so that
approximately one in five control group firms are adding or subtracting workers from one round
to the next. Since this is churn over a six month period, it suggests that many control group firms
are able to adjust their employment rapidly.
The next two panels of Table 5 examine econometrically this churn. We see a positive and
significant impact on the likelihood of adding a worker during the subsidy period, but a negative
and significant impact on the likelihood of adding a worker during the period two years after the
18
intervention. That is, post-subsidy, firms in the treatment group are slower to add workers during
a period when firms in the control group are growing. In contrast, the impact on subtracting
workers is not as dramatic as seen in Figures 3 and 4, and while positive immediately after the
intervention, is not statistically significant. Graphically we see that this subtraction effect occurs
in the six months immediately after the subsidy ends, and by averaging over the first year we
average in also the lower chance of subtracting a worker between 6 and 12 months post-
intervention.
The final two panels of Table 5 consider whether the change in paid workers is changing the other
two labor inputs in the business: the owner’s own time, and unpaid labor. On average, firms have
only 0.2 unpaid workers, and treatment has no significant impact on this number during any of our
follow-up periods. The point estimates on own hours are positive, but small and not statistically
significant during the intervention. The positive effect is significant for the two- and three-to-four-
year follow-up periods, and reflects the greater survival of firms at this stage. Taken together, these
results show that the subsidized labor is not substituting for other types of labor the business is
already using, but represents a net increase in labor input during the subsidy period.
Appendix 6 explores the extent to which the wage subsidy changes which firms have workers. The
evidence suggests that the new firms induced to hire an employee because of the subsidy, but who
would not have hired one if they had been in the control group, are smaller and less profitable
firms, and less likely to be found in Colombo. There is little selectivity on owner’s characteristics.
Conditional on hiring a worker, those in Colombo are more likely to have kept the worker on, with
no significant differences in other firm or owner characteristics. By the time of the last survey,
when we have seen the proportion of firms to have employees is similar in both groups, some of
these lower profitability treated firms no longer have a worker, while some of the lower
profitability control firms have started hiring one. The result is that baseline profit levels, and other
firm characteristics, are similar for the sample of treatment and control firms with workers at the
time of the last survey. The one remaining difference is in terms of geography, where a smaller
share of the treated firms with employees are in Colombo compared to the control group.
5.3 Impact on Profitability and Sales
We next examine how the wage subsidy and additional labor affected business profits and sales.
There are two important issues that affect measurement of the treatment effect on these outcomes.
19
The first, as discussed above, is the treatment impact on business survival post-intervention. We
consider both unconditional profits and sales (where firms not in operation are coded as having
zero profits and zero sales), and conditional measures (conditioning on the business operating).
Comparing outcomes for treated and control firms will only yield unbiased estimates of the impact
on conditional profits and sales if survival is not selective on characteristics that predict these
outcomes. We cannot reject that survival is independent of baseline characteristics (a joint test of
orthogonality for the sample still self-employed in round 12 has p-value 0.562), so this may be a
reasonable assumption in our case. Otherwise the conditional regressions should be viewed as
descriptive, rather than causal. Second, both profits and sales have long right tails: the 99th
percentile conditional on operating is six to eight times the mean, and kurtosis values of 14 to 20
(compared to 3 for a normal distribution). We use two approaches to reduce the dependence on
the top tail. The first is to consider transformations which place less weight on the top tail: the
inverse-hyperbolic sine transformation of unconditional values, and the log transformation of
conditional values. The second is to estimate quantile regressions.11
Table 6 presents the estimated treatment effects on these different measures, while Figures 5 and
6 graph the quantile treatment effects for round 4 and round 12 (during the intervention, and in our
last follow-up round four years later). For profits we see no significant effect during the
intervention period for any of the four measures, and the quantile treatment effects on both
conditional and unconditional profits are fairly constant and also not significant across the
distribution. The 95 percent confidence interval for the OLS treatment effect for unconditional
profits is (-1766, 3118), while for the 50th percentile it is (-1208, 3140). This is relative to a control
mean of 16,603 LKR, so represents a range of -11% to +19%. The impact on profits continues to
be insignificant in all three post-intervention periods for three out of four measures in Table 6, and
we cannot reject the hypothesis that all treatment effects are jointly zero. The exception is the
inverse hyperbolic sine transformation. This shows a positive treatment effect, which arises from
the survival effect at the bottom of the distribution, with positive treatment effects for lower
quantiles. Conditional on operating, this effect is not significant.
For sales we likewise see no significant treatment effect during the intervention using any of the
four measures, nor using the quantile treatment effects. The 95 percent confidence interval for
11
We control for the same baseline controls in the quantile regressions as in the OLS treatment regressions.
20
unconditional sales is (-8525, +19401), or (-14%, +32%) relative to the control mean. Like profits,
the inverse-hyperbolic sine transformation of sales then shows a significant treatment effect in the
post-intervention period, reflecting the impact on survival. We find a marginally significant effect
on unconditional sales in year 2, and on log sales in year 1 post-intervention, but in both cases
cannot reject that all treatment effects are jointly zero.
5.4 Return to Labor
We now can combine the impact on the number of workers with the impact on profits to obtain an
estimate of the return to additional labor in these microenterprises. For comparison, we begin by
using the pooled cross-sections from the control group sample to estimate for firm i in periods
t=2,…,12:
, ∗ , ∑ 1 ′ , (6)
Where L is the number of paid workers, and we control for time dummies, the variables used to
form strata for randomizing, and the baseline variables used in re-randomization as before. The
standard errors are clustered at the firm level. Column 1 of Table 7 shows this estimate using the
unconditional level of profits as the outcome, while column 5 uses log profits (conditional on
operating). We see an additional worker is significantly associated with higher profits, with firms
with one more worker earning 6,674 per week more profits, or 24 percent higher profits.
The standard concern with such an estimate is that there are unobserved features of the firm that
are correlated with both profitability and how many workers the firm hires. For example, more
productive firms may earn more and use more labor. We can control for time-invariant unobserved
firm characteristics by adding firm fixed effects to equation (6). Columns 2 and 6 of Table 7 do
this. Adding these fixed effects reduces the magnitude of the coefficient on labor to 4,844 or 13
percent, which is still statistically significant. However, this will still overstate the return to labor
if there are time-varying unobservables which lead firms to both hire more workers and be more
profitable: for example, a positive demand shock may cause the firm to be able to sell more and
hire more workers to meet this demand.
Our experiment provides an estimate of the causal effect of hiring an additional worker. Since the
intervention period is the only period during which we see a significant increase in the number of
workers, we estimate equation (6) only during the intervention period (t=4 and 5), and instrument
21
L with assignment to the wage subsidy treatment. Columns 3,4, and 7 of Table 7 then report the
IV estimates, under the assumption that the wage subsidy only affects profits through the additional
labor it induces. The point estimates are smaller than the fixed effects in levels, and similar in size
to the fixed effects estimates in logs; however, the standard errors are much larger. The point
estimates suggest a return of 2,400 to 3,000 LKR per month per additional worker hired. In panel
B we also include the other treatment groups which received wage subsidies in an effort to reduce
these standard errors, and get a 95 percent confidence interval of (-5310, +7612) for the impact on
profits conditional on operating. Recall that the wage subsidy was 4,000 LKR per month during
this time, and is not included in the measure of profit being reported by the owner. This point
estimate would suggest that the net return to keeping these workers at their current wages would
be negative once the subsidy was removed.
6 Mechanisms
The wage subsidies induced firms to hire additional workers during the intervention period, but
did not have a lasting impact on employment, nor a significant impact on profits and sales. They
did however make firms more likely to survive. We examine possible explanations for these
impacts in this section.
6.1 Heterogeneity of Treatment Effects
Our theory suggests several possible channels through which a short-term subsidy may have a
lasting impact on employment. We examine the heterogeneity of treatment effects to provide some
insights into whether these different channels appear to be operating in practice. To do this, we
add interactions between the treatment variables and a particular baseline covariate X to equation
(5), along with controlling for the baseline value of X, and interactions between X and the survey
round effects. The results are then presented in Table 8, which tests for heterogeneity in the impact
on the number of paid workers for different Xs.
If the subsidy allows firm owners to learn about their management type, θ, then we would expect
the impacts to be greater for younger firms (where the owners have had less time to learn their
type), and for firms whose owners have never hired a worker before. The first two columns of
Table 8 show that there is no significant heterogeneity with respect to either variable. Moreover,
the coefficients, indicate that that those who had hired workers before were more likely to hire
22
workers in response to the intervention the opposite sign to what the learning-about-type theory
would predict.
Column 3 of Table 8 examines heterogeneity with respect to baseline business practices.
Consistent with the higher take-up seen in Table 3, we see that firm owners with more management
ability were more likely to hire workers in response to the subsidy during the intervention. A one
standard deviation improvement in baseline practices (5.9) is associated with a 0.19 additional
worker increase during the intervention, which is significant at the five percent level. However,
like the aggregate effect, this effect dissipates over time and there is no long-term effect. Our
theory section noted that higher managerial ability firms might be more responsive to subsidies
because of non-convexities in hiring labor. Our wage subsidy required firms to hire a full-time
worker, so the margin for adjusting labor was lumpy. Better managed firms should be closer to the
threshold of hiring a whole worker, so may have responded more. An alternative explanation is
that firm owners with higher management ability could better understand the short-term gains
possible through the subsidy.
Columns 4 and 5 of Table 8 then examine heterogeneity with respect to wealth. If firms need
capital to make new workers productive, then the theory predicts that treatment effects should be
higher for firms which have more access to capital. We see no heterogeneity with respect to either
baseline capital stock, nor to household wealth at baseline.
Finally, in columns 6 and 7 of Table 8 we examine whether coupling the wage subsidy with
additional treatments increases the impact. Column 6 considers the business training treatment.
The specification here adds to equation (5) the pure treatment effects of business training in each
of the time periods (not shown), and then the interactive treatment effect of receiving both the
wage subsidy and business training. We cannot reject that the treatment effect is the same for those
who get business training. Column 7 likewise shows there is no differential effect for those who
get the savings treatment. These results are consistent with the interactions with baseline variables
in showing that the lack of long-run effects do not seem to be due to lack of capital or lack of
business skills.
6.2 Survey Evidence
23
Our survey data provide additional information which can help us interpret the results in Tables 5
through 8. The fact that subsidies have a temporary effect and that there is little evidence that the
increase in profits is greater than the subsidy amount suggests that labor markets work without
major frictions for the micro enterprises in our sample. This picture is consistent with the view that
urban informal labor markets working reasonably well. One of the advantages of experiments is
that they create shocks to opportunities that allow researchers to observe how actors respond. The
survey data provide details that help us understand the aggregate responses we observe in Tables
5-8.
We begin by looking at responses as they relate to key aspects of the heterogeneity examined in
Table 8.
Learning about type and managerial ability: Did owners learn about their types, for
example, did they learn about their ability to manage workers? Among those with a worker
hired under the program who left, we asked which among several reasons the worker left.
One option was that the owner had come to realize he was not able to properly manage the
worker. Across several rounds and more than 30 such cases, this reason was only ever
given once. There is a somewhat larger sample of owners who were eligible for the subsidy
but never hired a worker. In October 2009, we asked these owners whether any of 12
reasons for not hiring were important in their case. Only 13.3 percent of the owners said
concern about their ability to manage an employee was a reason for not hiring. The far
more common responses for not hiring related to a lack of demand for labor, including that
the additional employee would not be profitable (43.4 percent), that the enterprise does not
require an additional employee (26.5 percent, and that the subsidy is not large enough (13.3
percent). Together, these data suggest that learning about managerial ability is not a central
issue among these firms; the lack of hiring appears mainly to reflect a lack of demand for
labor. However, we note that a sizeable number of respondents not hiring workers stated
that they had not yet found the right employee (22.3 percent) or that they lacked the capital
required to make the employee productive (27.1 percent). Hence, these data do indicate
some potential role for search frictions and capital constraints.
Importance of access to capital: Among those not hiring workers, responses from the
October 2009 survey indicate that only 40 percent would need to make a capital investment
24
to make the additional employee profitable. Among these 40 percent, a majority (56
percent) say that a lack of capital is an important reason they did not hire anyone under the
program. Note that the likelihood an owner reports that capital is a reason for not hiring is
independent of either baseline profits or capital stock. Those with low profits and low
capital stock are no less likely to hire under the program, though as we noted in Section 4.2
above, they are more likely to hire relatives and workers at very low rates of pay. In April
2010, we asked about the same issue with a different framing, asking how much capital
would be required to make a new employee “as productive as (s)he could be.” Only 7
percent of respondents said “zero” to this question, but 43 percent said 15,000 LKR or less,
a level which is approximately one month’s profit for the average firm. Only 22 percent
said that more than 90,000 LKR – six months’ average profit – would be required. Though
suggesting that a lack of capital plays a role in some cases, these data are consistent with
the lack of any additional effect when the savings subsidy program is combined with the
wage subsidy program.
The survey data also yield some information on several other constraints suggested by theory.
Newly-hired employees have lower productivity: This, combined with either formal or
informal minimum wages might require that wage payments exceed the marginal
contribution of the employee for some period of time. In those circumstances, the subsidy
may induce firms to hire when they are otherwise unable to pay an interim wage that
reflects the lower marginal productivity of workers during the initial period working in the
firm. In April 2010, we asked owners how long they thought it would take a hired worker
to become fully productive. The median response was one month, and the mean 4.1
months; 86 percent said the period would be six months or shorter, suggesting that the
subsidy was long enough to fully cover the learning period for the majority of the sample.
In October 2011, we asked owners how long it took for the most recent worker they had
hired (if there was one) to be profitable for the enterprise. Focusing on employees hired
after the subsidy period, half the owners said the employee was profitable right away, and
another 38 percent said they were profitable within the first month. Only 2 percent said it
took six months or more. Hence, the survey data do not suggest that the time taken to
integrate an employee is long enough to explain the patterns we see in the data.
25
The relevance of search costs: In October 2009, three months after the wage subsidy offer
was made, we asked those eligible for the wage subsidies a series of questions related to
search. At the time of the survey, 29 percent of those eligible had hired an employee,
indicating they were able to find someone fairly quickly. Another 43 percent indicated that
they had no intention of hiring an employee.12 Among the remaining 29 percent of owners
who indicated they were still searching and expected to hire an employee, only 38 percent
(representing 11 percent of the sample) indicated that a reason for not hiring was that they
had not found the right employee. The majority indicated instead that at present the
additional employee would not be profitable given the subsidy level. These data suggest
that search costs are not a main constraint for the majority of owners in our sample. This
conclusion is supported by data from a survey of owners of small and medium sized
businesses conducted around the same time.13 In April 2009, among 160 owners with five
or fewer employees, the median owner said it would take seven days to locate an employee
if s/he wanted to hire one; the mean search period was 14 days. Moreover, these owners
said they could hire a worker for a median of 400 LKR per day, or 2,000 LKR per week,
just above the average wage the employees hired under our subsidy program report being
paid. That search costs are important for only a small percentage of owners of small firms
is consistent with long-held views that labor markets work relatively well among informal
firms. This is perhaps not surprising given that most workers are hired to do relatively
routine, physical tasks. Our owners say that the sex of the worker and physical strength of
the worker are the two most important characteristics of workers they consider hiring, with
education the least important of the characteristics listed. Search tends to be local, with a
majority of workers hired being previously known to owners and living within one
kilometer of the business.14 We read these responses together with the response reported
earlier just under a quarter of the owners eligible for the wage subsidy report not being able
12
These owners said in response to later questions that their business would not support or benefit from an additional
employee. Only 11 percent of them indicated that the inability to find the right employee was a reason for not hiring.
13
The SME survey was conducted in urban areas throughout Sri Lanka, but a majority of respondents come from the
same urban areas in which we conducted the experiment. The survey is described in Appendix 4.
14
The local nature of search holds both in these data and in data from a separate survey of wage workers. In the wage
worker survey, among 171 workers in firms with 4 or fewer employees, 61 percent say they knew the owner before
beginning work, and 45 percent say they live within one kilometer of the business. The wage worker surveys is
described in Appendix 4.
26
to find the right worker 3 months after learning of their eligibility as indicating that search
frictions are important for a minority of the owners, but are not a main cause of not hiring.
Finally, the excess hiring that was created by the subsidy largely disappears within a year of
withdrawing the subsidy. In most of the surveys conducted after the intervention, we asked the
employers whether the employee hired under the program was still working for them, and if not,
why they were not. The most common response was that the worker quit, given just over half the
time. In those cases, the owner reports taking over the worker’s tasks himself in 59 percent of the
cases, hiring another employee 29 percent of the time, and having a family member do the work
in 12 percent of the cases.
6.3 Why was there a survival impact?
The only long-term impact of the wage subsidies appears to be on firm survival, with no impact
on paid employment, sales or profitability. The evidence presented above suggests that the survival
impact is not coming through relieving labor market constraints on firms. Instead, the most likely
explanation for the survival effect appears to be that the subsidy provided firms with extra profits
during the intervention period, and this small amount of additional capital allowed firms to survive
shocks that would otherwise shut them down. De Mel et al. (2012) show one-time grants of 10,000
and 20,000 SLK helped small firms survive. If workers earn their marginal product, then the
maximum subsidy for a firm was 28,000 SLK. These firms are larger on average than those in De
Mel et al. (2012), so this amount is equivalent to less than two months of baseline profits. If it were
to have an effect, it should therefore be for the smallest firms. Appendix 7 provides heterogeneity
analysis that shows the survival effect is larger for firms with below median baseline capital and
below median profitability, although results are at most significant at the 10 percent level. We
therefore view this evidence as suggestive, but consistent with the survival effect coming through
a credit rather than labor market channel.
7 Discussion and Conclusions
Microenterprises in developing countries face many potential constraints to growth, and
understanding which of these constraints are binding is crucial for designing policies to address
them. Moreover, as firms with fewer than five employees are the source of livelihoods for the
majority of urban workers in most low- and middle-income countries, binding constraints to their
27
growth may have important aggregate effects on economies. This is particularly true with regard
to employment growth. Compared with a larger literature on capital and entrepreneurship training,
there is a paucity of research on the functioning of the informal labor markets most relevant to
these firms. We use a shock to wages, implemented through temporary subsidies offered when
enterprises hire new workers, to measure frictions in urban informal labor markets in Sri Lanka.
Data from the experiment suggest that labor markets function with modest frictions for these firms.
The effects of the subsidy are consistent with well-functioning neo-classical labor markets. Firms
respond to the subsidy by hiring additional workers, but the excess hiring dissipates completely
within a year or so of the removal of the subsidies. Complementary experiments loosening credit
constraints and providing entrepreneurship training do not change the effects of the temporary
subsidies. We conclude that hiring frictions are not an important constraint to firm growth in our
setting.
An obvious question is how much the results from this experiment generalize to the broader
development context. We suspect that many characteristics of this labor market hold in most urban
areas in developing countries. Workers remain unregistered and hiring is generally unregulated.
The work performed by employees in small enterprises involves relatively more brawn and less
creative energy. Employees are hired from local areas and there is usually a low degree of
separation between employer and employee before hiring. There are other aspects of the context
which are likely less usual. Our experiment coincided with the end of a long civil war in Sri Lanka,
and a period of rapid growth. Compared with other low- and middle-income countries, our samples
of both microentrepreneurs and wage workers show relatively high levels of generalized trust.15
How much these more distinctive features of the context drive the results is difficult to say. We
would hope this might be resolved by future work examining labor market frictions in different
contexts.
References
15
In April 2009 surveys. 32 percent of wage workers and 27 percent of entrepreneurs said that “most people can be
trusted.” Though this may seem low, it compares with rates in the general population in most Sub-Saharan African
and Latin American countries, where less than 20 percent of the population respond similarly. [Calculations by
authors using WVS data downloaded from http://www.worldvaluessurvey.org .]
28
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30
Figure 1: Impact on Firm Survival over Time
1 .95
Proportion self-employed
.85 .9.8
2 4 6 8 10 12
Survey round
Wage subsidy treatment Control
Notes: vertical lines indicate period during which wage subsidy was in effect. Round 2 is baseline
for half the sample and first follow-up for the other half.
31
Figure 2: Impact on Employment
Proportion with a Paid Worker Number of Paid Workers
.8
.4
.6
Proportion with a paid worker
Number of paid workers
.3
.4
.2
.2
.1
0
2 4 6 8 10 12 2 4 6 8 10 12
Survey Round Survey Round
Wage Subsidy Group Control Group Wage Subsidy Group Control Group
Notes: vertical lines show intervention period. Number of workers truncated at 5 workers. Round
2 is baseline for half the sample and first follow-up for the other half.
32
Figure 3: Employment Churn
Added a worker Subtracted a worker
.3
.2
.25
Proportion subtracting a worker
Proportion adding a worker
.2
.1
.15 .1
.05
0
2 4 6 8 10 12 2 4 6 8 10 12
Survey round Survey round
Wage Subsidy Group Control Group Wage Subsidy Group Control Group
Notes: vertical lines show intervention period. Addition and subtraction of workers are defined in
terms of changes in the total number of paid workers the firm has between one survey round and
the next.
33
Figure 4: Churn in the Number of Workers
Change in Workers R3 to R4 Change in Workers R5 to R6
.8
.8
.6
.6
Fraction
Fraction
.4
.4
.2
.2
0
0
-4 -2 0 2 4 6 -5 0 5
Change in Number of Workers Change in Number of Workers
Treatment Control Treatment Control
Notes: R3 to R4 is the change in the number of workers between the last pre-intervention survey
and first survey during the wage subsidy. R5 to R6 is the change in the number of workers between
the last survey during the intervention and first survey after the intervention.
34
Figure 5: Quantile Treatment Effects on Profits in Round 4 (During Intervention) and Round 12 (4 years later)
Round 4 Unconditional Profits Round 4 Conditional Profits
10000 20000
10000 20000
Conditional Profits
Profits
0
0
-10000
-10000
5 10 20 30 40 50 60 70 80 9095 5 10 20 30 40 50 60 70 80 9095
Percentile Percentile
Round 12 Unconditional Profits Round 12 Conditional Profits
20000 40000
20000 40000
Conditional Profits
Profits
0
0
-20000
-20000
5 10 20 30 40 50 60 70 80 9095 5 10 20 30 40 50 60 70 80 9095
Percentile Percentile
Notes: solid line shows quantile treatment effects, with 95% confidence interval around it. Dashed line indicates OLS treatment effect. Quantile regressions control
for baseline profits, randomization strata, and the set of re-randomized variables. Unconditional profits include zeros for firms not operating; conditional profits
are conditional on the business still operating.
35
Figure 6: Quantile Treatment Effects on Sales in Round 4 (During Intervention) and Round 12 (4 years later)
100000 Round 4 Unconditional Sales Round 4 Conditional Sales
100000
Conditional Sales
Sales
0
0
-100000
-100000
5 10 20 30 40 50 60 70 80 9095 5 10 20 30 40 50 60 70 80 9095
Percentile Percentile
Round 12 Unconditional Sales Round 12 Conditional Sales
100000
100000
Conditional Sales
Sales
0
0
-100000
-100000
5 10 20 30 40 50 60 70 80 9095 5 10 20 30 40 50 60 70 80 9095
Percentile Percentile
Notes: solid line shows quantile treatment effects, with 95% confidence interval around it. Dashed line indicates OLS treatment effect. Quantile regressions control
for baseline profits, randomization strata, and the set of re-randomized variables. Unconditional profits include zeros for firms not operating; conditional profits
are conditional on the business still operating.
36
Table 1: Balance at Baseline and Endline
Full Sample Normalized Present in Round 12 Normalized
Control Treatment p‐value Difference Control Treatment p‐value Difference
Re‐randomized Variables
Number of Paid Workers 0.19 0.16 0.498 ‐0.059 0.18 0.13 0.255 ‐0.092
Education (Years) 10.35 10.25 0.641 ‐0.040 10.35 10.23 0.604 ‐0.050
Raven Test Score 3.34 3.34 0.983 0.002 3.31 3.28 0.874 ‐0.015
Digitspan Recall Score 6.42 6.36 0.628 ‐0.042 6.43 6.39 0.786 ‐0.031
Total Assets 239893 250563 0.768 0.026 246815 248026 0.771 0.003
Total Assets<1500LKR 0.06 0.02 0.062 ‐0.164 0.06 0.02 0.022 ‐0.218
Total Assets>935000LKR 0.05 0.06 0.864 0.015 0.06 0.06 0.733 0.005
Monthly Profits 13862 14552 0.509 0.057 13916 14485 0.448 0.047
Profit Data Missing 0.03 0.02 0.348 ‐0.082 0.03 0.02 0.486 ‐0.058
Monthly Profits<2000LKR 0.06 0.03 0.179 ‐0.118 0.06 0.03 0.240 ‐0.099
Monthly Profits>30000LKR 0.04 0.06 0.257 0.098 0.04 0.06 0.342 0.074
Business Practices Score 8.27 8.76 0.343 0.082 8.32 8.78 0.429 0.079
From booster sample 0.52 0.53 0.841 0.017 0.53 0.54 0.906 0.032
Stratification Variables
Retail Sector 0.39 0.38 0.857 ‐0.016 0.39 0.39 0.974 ‐0.001
Colombo 0.47 0.44 0.436 ‐0.068 0.46 0.41 0.317 ‐0.105
Kandy 0.47 0.48 0.893 0.012 0.48 0.50 0.736 0.041
Additional Variables
Any paid worker at baseline 0.12 0.10 0.388 ‐0.075 0.12 0.08 0.119 ‐0.129
Monthly Sales 41175 52435 0.048 0.171 42079 52142 0.070 0.152
Owner's Age 35.43 35.16 0.644 ‐0.040 35.34 35.37 0.995 0.006
Business is Registered for Taxes 0.31 0.32 0.827 0.019 0.31 0.32 0.916 0.008
Weekly hours worked 57.94 59.31 0.379 0.076 58.23 58.55 0.940 0.018
Sample Size 286 250 262 230
Joint orthogonality p‐value 0.734 0.649
Note: present in round 12 denotes information on whether they have a paid worker is available in the last survey round.
37
Table 2: Data Availability by Treatment Status and Timing
Before During After Subsidy
Subsidy Subsidy Year1 Year2 Year3+
Panel A: Data on Operating Status Available
Control Group 0.958 0.951 0.983 0.986 0.976
Wage Subsidy Treatment 0.980 0.956 0.976 0.964 0.972
p‐value 0.148 0.787 0.596 0.099 0.799
Panel B: Data on Having a Paid Worker Available
Control Group 0.839 0.951 0.965 0.962 0.962
Wage Subsidy Treatment 0.888 0.956 0.948 0.920 0.956
p‐value 0.102 0.787 0.333 0.040 0.748
Panel C: Data on Profits Available
Control Group 0.808 0.944 0.965 0.965 0.962
Wage Subsidy Treatment 0.832 0.956 0.944 0.920 0.956
p‐value 0.467 0.529 0.241 0.024 0.748
Notes: Before Subsidy refers to round 3 data between baselines and
intervention. P‐value is from t‐test of equality of response rates between
control and wage subsidy treatment. Proportions shown indicate that data
are available for at least one survey round during the specified timing window.
Profits and Workers are set to zero for firms which are closed down.
38
Table 3: Correlates of Take‐up
Wage Subsidy Only Sample Any Wage Subsidy Treatment
Retail ‐0.084 ‐0.102* 0.001 ‐0.016
(0.055) (0.055) (0.030) (0.030)
Colombo ‐0.196** ‐0.134 ‐0.210*** ‐0.155***
(0.092) (0.094) (0.054) (0.055)
Kandy ‐0.067 ‐0.037 ‐0.145*** ‐0.117**
(0.091) (0.092) (0.054) (0.054)
Formally registered ‐0.006 ‐0.014 0.030 0.016
(0.060) (0.057) (0.031) (0.031)
Any paid worker at baseline 0.089 0.042 0.034 0.004
(0.086) (0.083) (0.046) (0.046)
Above median assets ‐0.018 ‐0.038 0.004 ‐0.019
(0.056) (0.053) (0.030) (0.030)
Firm five years or younger 0.067 0.066 0.026 0.025
(0.054) (0.053) (0.029) (0.030)
Owner's education (years) 0.020* 0.016 0.014** 0.012*
(0.011) (0.011) (0.006) (0.006)
Baseline business practice index 0.011*** 0.011*** 0.011*** 0.010***
(0.004) (0.004) (0.002) (0.003)
Owner's age ‐0.002 0.001 0.001 0.002
(0.004) (0.004) (0.002) (0.002)
Sample Size 250 250 250 843 843 842
Pseudo‐R2 0.044 0.050 0.083 0.020 0.036 0.047
Notes: coefficients are marginal effects from probit estimation. Robust standard errors in
parentheses. *, **, and *** denote significance at the 10, 5, and 1 percent levels respectively.
39
Table 4: Impact on Firm Survival
Sample Before During After Subsidy p‐value p‐value
Size Subsidy Subsidy Year1 Year2 Year3+ equality all zero
Panel A: Self‐employed in Survey Round
Assigned to Treatment 5005 ‐0.005 ‐0.009 0.056*** 0.074*** 0.058** 0.004 0.006
(0.023) (0.018) (0.021) (0.025) (0.027)
Control Mean 0.927 0.958 0.888 0.858 0.834
Panel B: Self‐employed, assuming that firms which close and are never observed again have stayed closed
Assigned to Treatment 5044 ‐0.006 ‐0.010 0.054** 0.066** 0.056* 0.009 0.014
(0.023) (0.018) (0.021) (0.026) (0.028)
Control Mean 0.927 0.958 0.888 0.855 0.817
Panel C: Self‐employed, assuming that all attritors are closed
Assigned to Treatment 5139 ‐0.008 ‐0.012 0.052** 0.058** 0.055* 0.015 0.029
(0.023) (0.018) (0.022) (0.028) (0.030)
Control Mean 0.888 0.879 0.820 0.827 0.788
Notes: robust standard errors in parentheses, clustered at the firm level. All regressions control for randomization
strata, variables used for re‐randomization, and contain survey round dummies.
*, **, *** indicate significance at the 10, 5, and 1 percent levels respectively.
p‐values are for test that the treatment effect is equal in the during, year 1, year 2, and years 3 to 4 periods; and that the treatment
effect is zero in all four periods.
40
Table 5: Impact on Employment
Before During After Subsidy p‐value p‐value
Sample size Subsidy Subsidy Year1 Year2 Year3+ equality all zero
Panel A: Number of Paid Workers
Assigned to Treatment 4824 ‐0.077 0.204*** 0.124 0.047 ‐0.023 0.043 0.027
(0.082) (0.075) (0.078) (0.080) (0.084)
Control Mean 0.48 0.48 0.45 0.51 0.60
Panel B: Any Paid Worker
Assigned to Treatment 4824 ‐0.014 0.140*** 0.111*** 0.024 ‐0.002 0.000 0.000
(0.036) (0.035) (0.034) (0.035) (0.032)
Control Mean 0.25 0.27 0.24 0.28 0.29
Panel C: Added a Worker Between Survey Rounds
Assigned to Treatment 4614 ‐0.008 0.109*** 0.015 ‐0.041** ‐0.003 0.000 0.000
(0.036) (0.024) (0.020) (0.020) (0.017)
Control Mean 0.19 0.11 0.10 0.14 0.13
Panel D: Subtracted a Worker Between Survey Rounds
Assigned to Treatment 4614 ‐0.022 ‐0.007 0.017 0.028 ‐0.005 0.413 0.546
(0.016) (0.019) (0.022) (0.020) (0.016)
Control Mean 0.05 0.11 0.14 0.10 0.11
Panel E: Own Hours Worked in the Business
Assigned to Treatment 4882 ‐0.580 0.664 2.919 3.932* 4.440** 0.423 0.189
(2.261) (1.910) (1.978) (2.076) (1.960)
Control Mean 47.3 51.3 44.0 45.0 42.8
Panel F: Number of Unpaid Workers in Business
Assigned to Treatment 4785 ‐0.045 0.008 ‐0.026 0.022 0.008 0.646 0.776
(0.047) (0.035) (0.044) (0.038) (0.037)
Control Mean 0.21 0.18 0.26 0.17 0.22
Notes: robust standard errors in parentheses, clustered at the firm level. All regressions control for randomization
strata, variables used for re‐randomization, the baseline value (except for panels C and D on churn), and contain
survey round dummies. *, **, *** indicate significance at the 10, 5, and 1 percent levels respectively.
Regressions are unconditional, and assign zero to the outcome for firms not operating.
p‐values are for test that the treatment effect is equal in the during, year 1, year 2, and years 3 to 4 periods;
and that the treatment effect is zero in all four periods.
41
Table 6: Impact on Profits and Sales
Before During After Subsidy p‐value p‐value
Sample size Subsidy Subsidy Year1 Year2 Year3+ equality all zero
Panel A: Unconditional Profits (Truncated at 99th Percentile)
Assigned to Treatment 4638 897 676 1863 1861 1483 0.798 0.523
(1487) (1246) (1159) (1454) (1179)
Control Mean 14572 16603 16557 18710 17854
Panel B: Inverse Hyperbolic Sine of Profits
Assigned to Treatment 4638 ‐0.022 0.203 0.590** 0.754*** 0.635** 0.265 0.086
(0.284) (0.217) (0.242) (0.284) (0.296)
Control Mean 9.21 9.38 8.97 8.86 8.56
Panel C: Profits Conditional on Business Operating (Truncated at 99th Percentile)
Assigned to Treatment 4159 1124 871 1017 633 530 0.987 0.931
(1539) (1269) (1174) (1499) (1219)
Control Mean 15954 17356 18658 21975 21588
Panel D: Log Profits Conditional on Business Operating
Assigned to Treatment 4120 0.076 0.045 0.061 0.011 0.005 0.812 0.835
(0.070) (0.058) (0.059) (0.061) (0.056)
Control Mean 9.39 9.45 9.55 9.71 9.72
Panel E: Unconditional Sales (Truncated at 99th Percentile)
Assigned to Treatment 4731 ‐4486 5438 6950 16652* 7256 0.457 0.417
(7326) (7124) (7763) (8846) (9410)
Control Mean 51783 60638 61625 69673 72910
Panel F: Inverse Hyperbolic Sine of Sales
Assigned to Treatment 4731 ‐0.046 0.196 0.740*** 0.882*** 0.677** 0.128 0.032
(0.299) (0.237) (0.252) (0.307) (0.319)
Control Mean 10.16 10.33 9.91 9.72 9.47
Panel G: Sales Conditional on Business Operating (Truncated at 99th Percentile)
Assigned to Treatment 4247 ‐4757 6636 4355 13817 4904 0.584 0.573
(7811) (7504) (8325) (9574) (10801)
Control Mean 56577 63361 69061 81830 88142
Panel H: Log Sales Conditional on Business Operating
Assigned to Treatment 4226 ‐0.009 0.103 0.140* 0.091 0.072 0.834 0.479
(0.087) (0.074) (0.079) (0.078) (0.081)
Control Mean 10.41 10.44 10.49 10.73 10.73
Notes: robust standard errors in parentheses, clustered at the firm level. All regressions control for randomization
strata, variables used for re‐randomization, the baseline value (except for panels C and D on churn), and contain
survey round dummies. *, **, *** indicate significance at the 10, 5, and 1 percent levels respectively.
p‐values are for test that the treatment effect is equal in the during, year 1, year 2, and years 3 to 4 periods;
and that the treatment effect is zero in all four periods.
42
Table 7: Return on Labor
LEVEL OF PROFITS LOG OF PROFITS
Associations in Associations in IV
Control Group Treatment IV estimates Control Group Treatment
Cross Panel Unconditional Conditional Cross Panel Effect
Section Data Profits Profits Section Data
Panel A: Using Wage subsidy Only Treatment for IV
Number of paid workers 6674*** 4844*** 2403 3054 0.216*** 0.122*** 0.138
(557) (575) (6055) (5697) (0.015) (0.017) (0.279)
Sample Size 4959 4959 951 905 4429 4429 884
Panel B: Using all groups which received a wage subsidy for IV
Number of paid workers 897 1151 0.140
(3530) (3297) (0.155)
Sample Size 1993 1888 1851
Notes: robust standard errors in parentheses, clustered at the firm level.
*, **, *** indicate significance at the 10, 5, and 1 percent levels respectively.
Regressions control for time fixed effects, randomization strata, and controls used in re‐randomization.
Columns 1, 2, 5, and 6 use control group only. Columns 3,4 and 7 use wage subsidy only and control groups in panel A,
and all groups receiving a wage subsidy in panel B.
43
Table 8: Heterogeneity in Impact on Number of Employees
Before Subsidy ‐0.178 ‐0.068 ‐0.127 ‐0.078 ‐0.111 ‐0.087 ‐0.073
(0.114) (0.062) (0.146) (0.112) (0.123) (0.083) (0.083)
During Subsidy 0.102 0.170** ‐0.079 0.136 0.155 0.191** 0.210***
(0.107) (0.069) (0.128) (0.096) (0.115) (0.075) (0.076)
Year 1 After 0.133 0.105 ‐0.135 0.059 0.075 0.112 0.129*
(0.100) (0.082) (0.147) (0.106) (0.126) (0.079) (0.078)
Year 2 After 0.021 ‐0.010 ‐0.137 ‐0.068 ‐0.025 0.035 0.052
(0.105) (0.081) (0.148) (0.109) (0.136) (0.081) (0.081)
Years 3‐4 After ‐0.043 ‐0.046 ‐0.046 ‐0.069 ‐0.072 ‐0.032 ‐0.017
(0.106) (0.089) (0.145) (0.121) (0.134) (0.084) (0.084)
Interaction with Young previously business above low household also assigned also assigned
firm hired practices median capital wealth business training savings treatment
Before Subsidy*Interaction 0.224 0.026 0.006 0.016 0.051 0.090 0.068
(0.159) (0.258) (0.014) (0.166) (0.163) (0.145) (0.139)
During Subsidy*Interaction 0.227 0.215 0.033** 0.145 0.078 ‐0.016 0.040
(0.149) (0.228) (0.014) (0.152) (0.150) (0.123) (0.131)
Year 1 After*Interaction ‐0.019 0.120 0.030** 0.144 0.082 ‐0.071 0.089
(0.158) (0.209) (0.015) (0.157) (0.156) (0.139) (0.142)
Year 2 After*Interaction 0.057 0.265 0.022 0.255 0.120 0.089 0.045
(0.162) (0.235) (0.016) (0.161) (0.164) (0.139) (0.148)
Years 3‐4 After*Interaction 0.045 0.133 0.002 0.105 0.083 0.059 0.066
(0.172) (0.227) (0.016) (0.166) (0.169) (0.135) (0.155)
Sample Size 4824 4824 4824 4824 4824 8742 8433
P‐value to test interactions all zero 0.377 0.788 0.063 0.565 0.989 0.677 0.986
Notes: robust standard errors in parentheses, clustered at the firm level. All regressions control for randomization strata, variables used for
re‐randomization and survey round. Columns 1 to 5 also control for baseline value of interacting variable and interaction between this
interacting variable and survey round. Columns 6 and 7 also control for business training and savings treatment effects respectively.
*, **, *** indicate significance at the 10,5, and 1 percent levels respectively.
Young firms are less than 5 years at baseline; low household wealth is based on a principal component of household assets. See appendix 4.
44
Online Appendices
Appendix 1: Timeline
April 2008 Round 1 - Screening Survey and Baseline I
October 2008: Round 2- Booster Sample and Baseline II
April 2009: Round 3
August 2009: Wage Subsidies Begin
October 2009: Round 4 (During Intervention)
April 2010: Round 5 (During Intervention)
May 2010: Wage Subsidies End
October 2010: Round 6
April 2011: Round 7
October 2011: Round 8
April 2012: Round 9
October 2012: Round 10
April 2013: Round 11
April 2014: Round 12
Supplementary Treatments:
Savings Treatment began November 2008, ended August 2009
Business Training Treatment: June-July 2009
Appendix 2: Further Details on Sampling
About half of our sample for this project comes from a larger panel survey which is representative
of all urban areas in Sri Lanka outside the northern province. From this panel survey, we selected
717 male self-employed workers with 2 or fewer paid employees in urban areas in Sri Lanka:
Colombo, Kandy and the Galle-Matara area. This part of the sample was constructed through a
listing exercise conducted in early 2008. We selected a total of 18 Division Secretariat (D.S.)
Divisions in the three urban areas. Within each D.S. Division we then selected 10 (in Colombo
and Kandy) or 5 (in Galle/ Matara) Grama Niladhara (GN) divisions and listed 50 households
45
starting from a random point.16 Because we needed a larger sample for the interventions, in October
2008 we selected a set of GNs neighboring those in the original panel survey. We used a similar
screening survey to identify male self-employed workers with fewer than 2 paid employees,
boosting the sample by 816 individuals. Because of the way they are constructed, both subsamples
are representative of the areas from which they are taken. However, there are some differences in
the manner of constructing them, so we add a control for the enterprises in the booster sample in
each of the regressions.17
Appendix 3: Details of Supplementary Interventions
Savings Intervention: In November 2008, we notified those assigned to the savings treatment that
they had been selected to participate in a program designed to encourage them to build savings
balances. The participants were not told about the other two interventions in November even if
they had been assigned to one of the other two treatments. As a part of the savings incentive
program, we offered to make the initial deposit in a savings account at the National Savings Bank
(NSB) and then to match deposits made into that account up to a certain limit each month and at a
pre-announced match rate. The account would remain ‘locked’ until August 1, 2009. The initial
match rate was set at 50 percent for deposits of up to 1,000 Sri Lankan Rupees (LKR)18 made by
the end of December. The match rate was kept at 50 percent through July, but the maximum
amount we would match was increased to 2,000 LKR in January and to 4,000 LKR in May 2009.
In July, we raised the match rate to 100% and the maximum to 5,000 LKR. Finally, just before the
accounts were unlocked, we added 5,000 LKR to every account, regardless of previous deposit
patterns. The participants received regular passbooks for the accounts, and deposits could be made
at any NSB branch. But the accounts were all opened through a single branch in Gampola so that
the branch manager there was able to ensure that money was withdrawn before August 1 only if
the participant faced an emergency situation. After the accounts were unlocked on August 1, the
participants were free to move the accounts to any NSB branch, or to withdraw the money. At that
16
The G.N. Division is the smallest of the four administrative levels in Sri Lanka: Provinces (9), Districts (25),
Divisional Secretariat (DS) Divisions (324), and Grama Niladhari (GN) Divisions (14,008).
17
We find no differences in the operating characteristics of the enterprises (sales, profits, etc.) but the owners in the
original sample have about a half year less schooling and have been in business for about three-quarters of a year
longer.
18
1,000 LKR was approximately US$8.75 in mid-2009, $8.85 in mid-2010, $9.14 in mid-2011, and $7.49 in mid-
2012.
46
point, we lost access the administrative data, and hence are unable to track when money was
withdrawn.
Training Intervention: This treatment was a training program based on the International Labor
Organization’s Improve Your Business (IYB) program. IYB is a five-day program intended to
generate growth in microenterprises. The modules covered are marketing, buying, costing, stock
control, record keeping, and financial planning. We asked that the training also include additional
material on hiring and managing employees, as employment generation is a key outcome of
interest in the project. The training was provided by the Sri Lankan Business Development Centre
(SLBDC),19 a Sri Lankan non-profit training institution established in 1984. SLBDC is the most
experienced provider of ILO entrepreneurship programs in Sri Lanka, having offered the first
training on the island in 2001. All of the SLBDC training staff involved in the project were
university qualified and trained under the national-level SIYB training programs conducted by the
ILO. Each had a minimum of five years of experience delivering SIYB training. Therefore, any
failure to find impacts should not be due to low quality trainers or inexperience with the materials.
Those selected for training were offered a stipend of 1,000 LKR and an additional bonus of 1,500
LKR paid at the end if they attended all five days. The stipend was meant to cover transport and
the opportunity cost of not working in the business on the training days.
Appendix Table 3 shows that assignment to these supplementary interventions is balanced
compared to the control group and wage subsidy only groups in terms of baseline observable
characteristics.
19
http://www.slbdc-lk.org/
47
Appendix Table 3: Balance for Supplementary Treatments
Control Wage Wage Subsidy Wage Subsidy Training Savings F‐test
Group Subsidy & Savings & Training Only Only p‐value
Re‐randomized Variables
Number of Paid Workers 0.19 0.16 0.20 0.15 0.23 0.25 0.507
Education (Years) 10.35 10.25 10.32 10.54 10.52 10.43 0.659
Raven Test Score 3.34 3.34 3.32 3.12 3.28 3.35 0.687
Digitspan Recall Score 6.42 6.36 6.35 6.39 6.27 6.21 0.681
Total Assets 239893 250563 232635 203654 236665 258261 0.430
Total Assets<1500LKR 0.06 0.02 0.03 0.03 0.01 0.05 0.135
Total Assets>935000LKR 0.05 0.06 0.04 0.03 0.04 0.05 0.743
Monthly Profits 13862 14552 14010 12947 13282 13861 0.491
Profit Data Missing 0.03 0.02 0.03 0.03 0.02 0.02 0.624
Monthly Profits<2000LKR 0.06 0.03 0.03 0.04 0.03 0.04 0.896
Monthly Profits>30000LKR 0.04 0.06 0.06 0.04 0.06 0.01 0.002
Business Practices Score 8.27 8.76 8.24 8.59 9.24 8.35 0.440
From booster sample 0.52 0.53 0.54 0.56 0.54 0.46 0.435
Stratification Variables
Retail Sector 0.39 0.38 0.38 0.38 0.38 0.38 1.000
Colombo 0.47 0.44 0.47 0.46 0.49 0.47 0.898
Kandy 0.47 0.48 0.47 0.47 0.48 0.47 1.000
Additional Variables
Any paid worker at baseline 0.12 0.10 0.13 0.09 0.15 0.12 0.385
Monthly Sales 41175 52435 49142 41785 46768 34496 0.013
Owner's Age 35.43 35.16 36.19 34.91 34.28 34.38 0.049
Business is Registered for Taxes 0.31 0.32 0.32 0.31 0.31 0.40 0.478
Weekly hours worked 57.94 59.31 60.77 60.41 57.20 59.78 0.496
Sample Size 286 250 297 298 141 112
48
Appendix 4: Measurement of Key Variables
Our key outcomes are measured as follows:
Survival: we examine survival in terms of whether the individual is self-employed at the time of
the survey. This includes those who have shut down their business and started a new one. It is
directly measured by asking whether they are engaged in self-employment on the survey, and
through direct observation and asking family and neighbors for those firms which attrit. Where the
original respondent cannot be located, beginning in round 7 (April 2011) we ask family members
or neighbors whether the individual still operates the business they previously operated. When the
alternative respondent says no, we ask them what the initial respondent is presently doing. In our
baseline specifications, we use responses from the first but not the second to define the survival
variable. We do this because we believe the information on whether the original business is still
operating is likely to be more reliable. An alternative approach would be to use both responses to
define whether the individual still operates any business. The results from this approach are
qualitatively similar, though the treatment effect in the second year after treatment is slightly larger
in magnitude. Regressions using this alternative definition are available from the authors on
request.
Number of Paid Workers: this is the number of permanent workers plus the number of casual and
daily workers reported on the survey. It is truncated at 5 workers (the 99th percentile) to reduce the
influence of outliers, and coded as 0 for firms that do not survive.
Any paid worker: defined as having at least one paid worker.
Added a worker between survey rounds: defined as the number of paid workers in round t
exceeding that in round t-1. It therefore measures net, rather than gross, worker flows.
Subtracted a worker between survey rounds: defined as the number of paid workers in round t
being less than in round t-1.
Own hours reported in the business: the number of hours worked in the business in the last week,
truncated at the 99th percentile, and coded as 0 for individuals not self-employed.
Number of unpaid workers in the business: Number of unpaid workers reported by the firm owner.
49
Firm profits: these are monthly, and were asked directly of the owner as “the total income of the
business during each of the last month after paying all expenses including wages of employees,
but not including any income you paid yourself”. This follows the wording and recommendation
of De Mel et al. (2009).20 We consider several transforms of profits to deal with outliers and firm
closure. This includes unconditional profits (which put zeroes in for closed firms) truncated at the
99th percentile, the inverse hyperbolic sine of profits, truncated profits conditional on the business
operating, and log profits conditional on operation. Nominal values were deflated to real values
using the Consumer Price Index for Colombo, gathered by the Sri Lankan Department of Census
and Statistics.
Firm sales: these are firm sales in the past month, deflated into real terms using the CPI. As with
profits, we consider several transforms of the raw data to account for outliers and firm closure,
with the variables defined analogously to profits.
Business Practices score:
The total score – the composite business practice score -- ranges from a minimum of -1 to a
maximum of 29. The total is the sum of the following component scores: the marketing score, the
stock score, the records score, and the financial planning score.
The marketing score ranges from 0 to 7, and it is calculated by adding one point for each of the
following that the business has done in the last 3 months:
Visited at least one of its competitor’s businesses to see what prices its competitors are
‐
charging
‐ Visited at least one of its competitor’s businesses to see what products its competitors have
available for sale
‐ Asked existing customers whether there are any other products the customers would like
the business to sell or produce
‐ Talked with at least one former customer to find out why former customers have stopped
buying from this business
‐ Asked a supplier about which products are selling well in this business’ industry
‐ Attracted customers with a special offer
‐ Advertised in any form (last 6 months)
The stock score ranges from -1 to 2, and it is calculated by subtracting one point
‐ If the business runs out of stock once a month or more
20
De Mel, Suresh, David McKenzie and Christopher Woodruff (2009) “Measuring Microenterprise Profits: Must
We Ask How the Sausage Is Made?”,Journal of Development Economics, 88(1): 19-31.
50
And adding one point for each of the following that the business has done in the last 3 months
Attempted to negotiate with a supplier for a lower price on raw material
‐
Compared the prices or quality offered by alternate suppliers or sources of raw materials
‐
to the business’ current suppliers or sources of raw material
The records score ranges from 0 to 8, and it is calculated by adding one point for each of the
following that the business does
‐Keeps written business records
‐Records every purchase and sale made by the business
‐Able to use records to see how much cash the business has on hand at any point in time
‐Uses records regularly to know whether sales of a particular product are increasing or
decreasing from one month to another
‐ Works out the cost to the business of each main product it sells
‐ Knows which goods you make the most profit per item selling
‐ Has a written budget, which states how much is owed each month for rent, electricity,
equipment maintenance, transport, advertising, and other indirect costs to business
‐ Has records documenting that there exists enough money each month after paying business
expenses to repay a loan in the hypothetical situation that this business wants a bank loan
The financial planning score ranges from 0-12, and it is calculated by adding up to three points
for each of the following two questions
How frequently do you review the financial performance of your business and analyze
‐
where there are areas for improvement
‐ How frequently do you compare performance to your target
o Zero points for “Never”
o One point for “Once a year or less”
o Two points for “Two or three times a year”
o Three points for “Monthly or more often”
And adding one point for each of the following that the business has
‐ A target set for sales over the next year
‐ A budget of the likely costs your business will have to face over the next year
‐ An annual profit and loss statement
‐ An annual statement of cash flow
‐ An annual balance sheet
‐ An annual income/expenditure sheet
Wage worker and SME surveys
We also make use of data from surveys of wage workers and larger firms. The wage worker survey
was conducted in all urban areas in Sri Lanka at annual intervals from 2008-2011. The initial
51
sample was drawn from a listing of households in randomly selected Grama Niladhari divisions.
The SME survey of larger firm owners selected surveyed firms with between 5 and 250 workers
(including the owner). This sample was drawn from a listing of visible enterprises conducted for
other purposes by the Sri Lanka office of AC Nielsen. We surveyed owners first in April 2008,
and resurveyed in April 2009 and April 2010. The questions from the wage worker and SME
surveys that we used in the analysis for this paper are described in the text.
Appendix 5: Round by Round Survey Attrition Rate
Appendix Figure 5 shows the attrition rate by round, in terms of whether we have information on
whether the business is still open/the owner is self-employed, and in terms of whether we can
measure whether the enterprise has paid workers. Starting in round 7 we added a module which
collected information from relatives, friends, and neighboring businesses if the business was not
able to be interviewed, resulting in a reduction in attrition at that time. The attrition rate averages
5.6 percent for data on whether the business is operating, and 9 percent for data on whether the
business has paid workers. Attrition rates are balanced for treatment and control in most waves,
and in the last round we have data on employment for all but 8 percent of firms.
52
Attrition rate on self-employment data
.15
Cumulative attrition in round
.05 0 .1
2 4 6 8 10 12
Survey round
SE data - Treat SE data - control
Employment data - Treat Employment data - control
Appendix 6: Does treatment change which firms have workers?
Appendix Table 6.1 compares the baseline characteristics of the subsample of treatment and
control firms which have a paid employee in round 4 (during the intervention), and in round 12
(the last survey round). This comparison allows us to see the extent to which the wage subsidy
changes which firms have paid workers. We see little selectivity in terms of owner’s education,
raven, and digit span scores. During the intervention, the firms hiring workers who would not have
done so if they were in the control group appear to be smaller (lower profits, lower total assets)
and outside Colombo. However, by the time of the last survey, the profit difference has
disappeared, and only the geographic difference remains.
53
Appendix Table 6.1: Does Treatment Change Which Firms Have Workers?
Have a Worker in Round 4 Have a Worker in Round 12
Control Treatment p‐value Control Treatment p‐ value
Number of Paid Workers 0.43 0.27 0.157 0.47 0.30 0.213
Education (Years) 10.17 10.33 0.682 10.60 10.63 0.943
Raven Test Score 3.19 3.23 0.891 3.08 3.08 0.985
Digitspan Recall Score 6.51 6.55 0.858 6.56 6.50 0.816
Total Assets 332819 280911 0.483 320187 349938 0.752
Total Assets<1500LKR 0.01 0.02 0.750 0.03 0.02 0.633
Total Assets>935000LKR 0.09 0.06 0.584 0.10 0.13 0.609
Monthly Profits 20500 15473 0.029 17927 17759 0.953
Profit Data Missing 0.01 0.02 0.750 0.03 0.02 0.633
Monthly Profits<2000LKR 0.03 0.01 0.394 0.07 0.02 0.129
Monthly Profits>30000LKR 0.09 0.07 0.778 0.06 0.08 0.600
Business Practices Score 8.79 10.19 0.146 9.64 10.30 0.541
From booster sample 0.53 0.58 0.523 0.49 0.53 0.602
Retail Sector 0.31 0.34 0.762 0.36 0.28 0.324
Colombo 0.50 0.33 0.024 0.47 0.30 0.037
Kandy 0.46 0.56 0.203 0.44 0.61 0.055
Any paid worker at baseline 0.29 0.18 0.105 0.29 0.17 0.102
Monthly Sales 57161 67089 0.414 49053 61765 0.276
Owner's Age 36.93 35.01 0.046 36.65 35.00 0.122
Business is Registered for Tax 0.37 0.26 0.139 0.35 0.27 0.307
Weekly hours worked 59.20 60.07 0.741 56.83 57.13 0.916
Notes: characteristics are baseline characteristics. P‐value compares whether characteristics of firms
having a paid worker in round 4 (during the intervention), and in round 12 (last survey) are similar
for the treatment and control groups using a t‐ test of equality of means.
Appendix Figure 6 explores further how the baseline profitability of those hiring workers during
the intervention period compares in the treatment and control groups, and to those who already
had workers and those who never hired a worker amongst the treatment group. We see the
treatment brings into hiring workers firms with lower profits than those hiring workers in the
control group, and than those who already had workers in the treatment group. Those hiring
workers in the treatment group have a similar baseline profits distribution to those who never hire
a worker during the intervention period.
Appendix Figure 6: Treated Firms Hiring Workers During Intervention Were Lower Profit
Firms
54
Firms with Workers in Round 4 Among treated, who hires workers?
.00005
.00008
.00004
.00006
Probability Density
Probability Density
.00003
.00004
.00002
.00002
.00001
0
0
0 20000 40000 60000 80000
Baseline profits
0 20000 40000 60000 80000
Baseline Profits
Always had worker
Treatment Newly added worker
Control Never have worker
Appendix Table 6.2 then looks within the treatment group to see how the baseline characteristics
of those who hire a worker during the intervention period and then reduce employment again
compare to those who hire a worker and maintain this new employment level for at least a year
after. The same is done for the control group, although only 8 control firms hire a worker and then
do not reduce employment again afterwards. We see few significant differences, suggesting that
those who keep the worker look quite similar on observable baseline characteristics to those which
do not. The one difference is again in terms of geography: although firms in Colombo were less
likely to respond to the wage subsidy, those that did hire workers were more likely to keep them
on afterwards than those in the other cities.
55
Appendix Table 6.2: Do the characteristics of firms which hire and keep workers differ from those which hire and let go?
Wage Subsidy Treatment Group Control Group
Hire and Hire and Hire and Hire and
Let Go Keep p‐value Let Go Keep p‐value
Number of Paid Workers 0.23 0.43 0.309 0.36 0.38 0.944
Education (Years) 10.38 9.87 0.434 10.00 10.38 0.683
Raven Test Score 3.11 2.91 0.694 2.91 3.88 0.202
Digitspan Recall Score 6.50 6.17 0.339 6.16 6.88 0.164
Total Assets 287603 244850 0.651 240620 571325 0.132
Total Assets<1500LKR 0.02 0.09 0.110 0.00 0.00 .
Total Assets>935000LKR 0.06 0.04 0.740 0.07 0.13 0.574
Monthly Profits 15167 15036 0.969 17197 19921 0.618
Profit Data Missing 0.02 0.04 0.450 0.00 0.00 .
Monthly Profits<2000LKR 0.02 0.00 0.552 0.04 0.00 0.552
Monthly Profits>30000LKR 0.06 0.04 0.740 0.04 0.00 0.552
Business Practices Score 9.81 8.17 0.315 8.22 10.88 0.227
From booster sample 0.59 0.65 0.627 0.53 0.50 0.865
Retail Sector 0.36 0.17 0.101 0.27 0.63 0.046
Colombo 0.31 0.57 0.032 0.49 0.63 0.487
Kandy 0.58 0.30 0.024 0.44 0.38 0.721
Any paid worker at baseline 0.16 0.13 0.769 0.22 0.25 0.866
Monthly Sales 56787 57263 0.981 49618 61307 0.552
Owner's Age 35.41 34.30 0.509 35.60 38.38 0.250
Business is Registered for Taxes 0.31 0.22 0.393 0.29 0.25 0.826
Weekly hours worked 59.94 58.74 0.770 57.51 62.50 0.482
Sample Size 64 23 45 8
Notes: Hire and Let go indicates the firm hired a worker during the intervention period (rounds 4 and 5), but then lowered
the number of employees compared to the previous round in one of round 4, 5, or 6. Hire and Keep indicates they hired a
worker and did not then reduce their number of employees in the first year after the intervention.
Appendix 7: Heterogeneity in Survival Impact
We estimate equation (5), adding treatment interactions, the baseline value of the interacting
variable, and the interactions between this interacting variable and survey round. We do this for
the outcome of business survival, and report the results in Appendix Table 7. The first column
shows no heterogeneity in the treatment effect on survival with respect to baseline business
practices. The second column shows that firms with initially low capital have a higher treatment
effect for survival. The interactions of treatment with above median baseline capital are significant
at the 10 percent levels in years 2, and years 3 and 4. The magnitude of the coefficients is almost
enough to entirely offset the treatment effect, suggesting the treatment effect only occurs for low
capital firms. Appendix Figure 7 shows this graphically: the control group sample with low
baseline assets dies at a faster rate over time than the control group sample with high baseline
assets, whereas the death rates for the low asset treated are similar to those of the high asset treated
56
and the high asset control. Nevertheless, a joint test that all interactions are zero cannot reject the
null hypothesis. Column 3 likewise shows higher point estimates for the treatment effect on
survival for firms with initially low profitability, with negative, but not statistically significant,
interaction effects with having above median profit.
Appendix Table 7: Heterogeneity in Survival
Before Subsidy ‐ 0.011 0.017 ‐0.023
(0.046) (0.038) (0.034)
During Subsidy 0.006 ‐0.012 ‐0.012
(0.031) (0.030) (0.028)
Year 1 After 0.052 0.075** 0.069**
(0.038) (0.032) (0.030)
Year 2 After 0.083* 0.114*** 0.097**
(0.046) (0.038) (0.038)
Years 3‐4 After 0.065 0.104*** 0.059
(0.049) (0.040) (0.040)
Interaction with business above above
practices median capital median profit
Before Subsidy*Interaction 0.001 ‐0.051 0.033
(0.004) (0.046) (0.048)
During Subsidy*Interaction ‐ 0.002 0.005 0.006
(0.003) (0.035) (0.037)
Year 1 After*Interaction 0.000 ‐0.042 ‐0.026
(0.004) (0.041) (0.043)
Year 2 After*Interaction ‐ 0.001 ‐ 0.085* ‐0.045
(0.004) (0.049) (0.051)
Years 3‐4 After*Interaction ‐ 0.001 ‐ 0.097* ‐0.000
(0.005) (0.052) (0.054)
Sample Size 5005 5005 5005
P‐value 0.962 0.368 0.785
Notes: robust standard errors in parentheses, clustered at the firm level.
All regressions control for randomization strata, variables used for re ‐ randomization,
survey round, baseline value of interacting variable and interaction between this
interacting variable and survey round.
*, **, *** indicate significance at the 10,5, and 1 percent levels respectively.
57
Appendix Figure 7: Heterogeneous Survival Effects by Baseline Capital
Survival over time by Baseline Capital
1
Proportion Still Selfemployed
.8 .85 .9 .95
2 4 6 8 10 12
Survey Round
Treated: High Assets Control: High Assets
Treated: Low Assets Control: Low Assets
Note: High Asset and Low Asset are defined as having above and below the baseline median
capital stock level respectively.
58