metadata: authors: 0: author: Chaudhary,Sarur
1: author: Sharma,Siddharth
count: India
docna: 0: docna: The Impact of Lifting Firing Restrictions on
            Firms : Evidence from a State-Level Labor Law Amendment
docty: Policy Research Working Paper
abstracts: cdata!: Stringent employment protection laws are
            argued to be a cause of reduced employment flexibility,
            slower growth and increased reliance on temporary employment
            contracts in many countries, including India. In 2014, the
            Indian state of Rajasthan amended labor laws to increase
            employment flexibility in firms. The most discussed of the
            amendments lifted the requirement for government approval
            for retrenching regular workers in medium-size factories.
            This paper first conducts a synthetic control analysis of
            the policy change using state-level panel data from 1980 to
            2018, finding no evidence of an impact on aggregate
            manufacturing employment and output. The paper then uses
            firm-level panel data to conduct a difference-in-differences
            analysis of the main amendment, exploiting its
            size-dependent feature for identification. This analysis
            finds that the amendment reduced the implicit regulatory
            cost of labor in firms, but there is no discernible impact
            on their total employment and output. The amendment also led
            to firms substituting temporary (“contract”) workers for
            permanent workers. This collateral impact is contrary to the
            expectation that easing the flexibility of permanent
            employment arrangements would make them more attractive to firms.
display_title: The Impact of Lifting Firing
            Restrictions on Firms : Evidence from a State-Level Labor
            Law Amendment
listing_relative_url: /research/2022/05/33813053/impact-lifting-firing-restrictions-firms-evidence-state-level-labor-law-amendment
topicv3: Private Sector Development m1326060 1921,Economic Growth m1326241 471,Structural Policy and Reform m1326450 1130,Investment Climate(IC) m1327235 401,Labor Market Analysis m1582757 4428
publishtoextweb_dt: 2022-05-09T00:00:00Z
dois: 10.1596/1813-9450-10039
origu: Off of Sr VP Dev Econ/Chief Econ (DECVP)
author_keys: 0: author_key: NA
1: author_key: 717230
model_extractions: Policy Research Working Paper 10039 The Impact of Lifting Firing Restrictions on Firms Evidence from a State-Level Labor Law Amendment _Sarur Chaudhary Siddharth Sharma_ South Asia Region Office of the Chief Economist May 2022
Policy Research Working Paper 10039

# **Abstract**

Stringent employment protection laws are argued to be a cause of reduced employment flexibility, slower growth and increased reliance on temporary employment contracts in many countries, including India. In 2014, the Indian state of Rajasthan amended labor laws to increase employment flexibility in firms. The most discussed of the amendments lifted the requirement for government approval for retrenching regular workers in medium-size factories. This paper first conducts a synthetic control analysis of the policy change using state-level panel data from 1980 to 2018, finding no evidence of an impact on aggregate manufacturing employment and output. The paper then uses firm-level panel data to conduct a difference-in-differences analysis of the main amendment, exploiting its size-dependent feature for identification. This analysis finds that the amendment reduced the implicit regulatory cost of labor in firms, but there is no discernible impact on their total employment and output. The amendment also led to firms substituting temporary (“contract”) workers for permanent workers. This collateral impact is contrary to the expectation that easing the flexibility of permanent employment arrangements would make them more attractive to firms.

This paper is a product of the Office of the Chief Economist, South Asia Region. 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://www.worldbank.org/prwp. The authors may be contacted at ssharma1@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._ Produced by the Research Support Team
# The Impact of Lifting Firing Restrictions on Firms: Evidence from a State-Level Labor Law

# Amendment

Sarur Chaudhary,<sup>_∗_</sup> Siddharth Sharma<sup>_†‡_</sup>

**Keywords–** Labor Laws, Business Regulation, Firms, Firm-level Employment, India JEL **Codes–** O12, K31, L50, J50, D22

- _∗_ University of Cambridge.

> _†_ Corresponding Author, The World Bank. Email: ssharma1@worldbank.org. The views expressed are those of the individual authors and do not necessarily reflect those of the World Bank Group.

> _‡_ We are grateful to Maurizio Bussolo, Ritam Chaurey, Arti Grover, Amit Khandelwal, Jean Nahrae Lee, Aaditya Mattoo, Hans Timmer and Hernan Winkler for helpful comments.
# **1 Introduction**

There is a great deal of debate on the impact of employment protection laws and other types of industrial labor regulation (as documented, for example, in Botero, Djankov, Porta, de Silanes and Shleifer (2004)). This issue is very salient in India given its plethora of industrial labor laws. Their impact on India’s economic performance is the subject of a large and influential body of research.<sup>1</sup> This research has focused on the Industrial Disputes Act (IDA), the law which governs the procedures for hiring and firing regular workers and the closure of factories. The IDA contains some extreme employment protection provisions. Its Chapter V-B, for example, requires official permission for any retrenchment, and a 90 day advance notice for closure, in any factory above a specified size threshold. Besley and Burgess (2004) suggest that such pro-worker provisions led to slower growth in India’s formal manufacturing sector and an increase in informality during 1958-1992. There is also evidence that firms have increasingly resorted to the use of temporary (“contract”) labor not subject to IDA to retain employment flexibility (Chaurey 2015).

This paper contributes to this literature by studying the effect of amendments to the IDA and certain other labor laws enacted by the Indian state of Rajasthan in 2014-15. The amendments were widely described as a major policy reform in the business press and government reports.<sup>2</sup> Some of them may be rolled out country-wide as part of a new federal labor code currently under consideration.<sup>3</sup> Rajasthan’s amendments present a rare opportunity to study a major change in labor law at the state level in India. This is because most prior studies of Indian labor laws have exploited an index coding the overall “pro-employer” or “pro-worker” tilt of each state’s IDA for empirical identification.<sup>4</sup> This reliance on an index aggregating heterogeneous IDA amendments has been critiqued for a number of reasons, including the disputable coding of specific IDA adjustments as being unambiguously pro-worker or pro-employer.<sup>5</sup> Moreover, since the IDA has not been amended significantly by any state after 1989, most index-based studies essentially rely on crossThe amendments made Rajasthan’s labor laws more pro-employer. Most prominently, the em-

> 1For example, Besley and Burgess (2004), Ahsan and Pag ́es (2009), Hasan R. and Ramaswamy (2007) Aghion, Burgess, Redding and Zilibotti (2008) and Adhvaryu, Chari and Sharma (2013). 2See, for example, G.o.India (2019) and Jha (2014).

> 3G.o.India (2020).

> 4The index was originally codified in Besley and Burgess (2004).

> 5See Bhattacharjea (2006) and Bhattacharjea (2019).

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ployment size threshold at which IDA Chapter V-B starts to apply to a factory was raised from 100 to 300 workers. The amendments also imposed more stringent minimum membership size requirements on unions. Furthermore, they exempted factories with fewer than 50 contract workers from the Contract Labor Act (CLA), the law which regulates the hiring of contract workers.

We first conduct a comparative case study of the amendments using the synthetic control method. This technique is suited for studying the aggregate impacts of changes that effect a small set of large economic units. It uses a weighted combination of potential comparison units -in our case, Indian states other than Rajasthan- as the control group, with the choice of weights being data-driven (Abadie and Gardeazabal 2003).<sup>6</sup> For this exercise, we use official state-level estimates of the formal manufacturing sector for the 1980-2018 period. The availability of 35 years of pre-treatment data is advantageous as it potentially improves the quality of the synthetic control.

The results suggest that contrary to expectations, the amendments did not have a sizable aggregate impact on employment and output in the formal manufacturing sector. There is some evidence of a positive impact on output, but it is not robust to standard checks.<sup>7</sup> Next, we use factory level panel data from 2010 to 2018 to conduct a difference-in-differences analysis of the main policy change, the repeal of IDA Chapter V-B. This strategy exploits the fact that the amendment affected factories with 100-300 workers.<sup>8</sup> We compare outcomes before and after the amendment across factories with 100-300 workers and those with more than 300 workers, across Rajasthan and other states. This comparison is important as there may have been nationwide shocks that varied systematically by firm size.

Consistent with the synthetic control results, the panel data analysis indicates that the IDA amendment did not affect total employment, output, capital and output per worker in treated firms.<sup>9</sup> But, there was a significant increase in their employment of contract workers. There is

> 6The synthetic control method has been used in comparative case studies across a wide range of contexts, such as tobacco taxation in California (Abadie, Diamond and Hainmueller 2010), German reunification (Abadie, Diamond and Hainmueller 2015), economic liberalization episodes (Billmeier and Nannicini 2013), natural disasters (Coffman and Noy 2012), affirmative action policies (Hinrichs 2012) and political connections (Acemoglu, Johnson, Kermani, Kwak and Mitton 2016).

> 7Having only three years of post-treatment data, we focus on outcomes such as employment and output that are likely to respond to the policy change within this relatively short time frame, as opposed to more long-term outcomes such as firm entry and investment.

> 8We are not the first paper to examine the impacts of Rajasthan’s amendments using firm level data. The amendments were first examined in an annual report of the government (G.o.India 2019). Goswami and Paul (2021) employ firm level data and panel analysis methods similar to that used in this paper to examine the amendments, with similar findings.

> 9We use the terms factory, manufacturing establishment and firm interchangeably; the primary unit of analysis is a factory.

2
also some evidence that treated firms reduced the employment of regular (non-contract) workers. Overall, the amendment increased the share of contract workers.

We also find that firms exempted from IDA Chapter V-B behaved as if they now faced a lower implicit regulatory tax on labor. We infer this implicit cost using a method based on the firm’s optimal cost minimization conditions which makes minimal assumptions on the production function and market demand (Chaurey, Manghnani, Perego and Sharma 2019).<sup>10</sup> We estimate a 13 percent reduction in the implicit labor tax, driven by a lower implicit tax on contract labor specifically.

We present a variety of robustness checks on these results regarding the contract labor share and the implicit labor tax. A dynamic event study specification confirms that the results are not due to differential pre-treatment trends across factories of different sizes. The results are robust to using only firms from neighboring states or states with similar per capita GDP in the control group. Speaking to the concern that firms may have strategically under-reported their employment in 2014-15 in anticipation of the policy change, we show that the main results are robust to redefining treatment status based on the firm’s average employment in the three most recent pre-treatment years.

The absence of an impact on total employment and output per worker is unexpected in light of the prevailing message in the literature that the IDA has stunted Indian manufacturing firms. However, it is worth noting that theory is ambiguous about the aggregate employment effects of reducing employment protection, at least in the short run. When labor adjustment becomes easier, labor flows should increase but the change in net equilibrium employment is not necessarily positive (Bentolila and Bertola (1999) and Hopenhayn and Rogerson (1993)).

The positive impact on contract hiring is more puzzling, since the IDA amendment should have reduced the relative appeal of contract workers. The obvious suspect behind this finding is the simultaneous easing of the threshold at which the CLA applies, since this law imposes certain restrictions on how contract labor may be used. But as we show, the estimated positive impact of the IDA amendment on contract hiring is larger among treated firms that still remained subject to the CLA, as compared to those newly exempted from it. Hence, the CLA amendment cannot explain our findings.

It could be that among firms with 100-300 workers, the repeal of IDA Chapter V-B was interpreted as a general relaxation in the enforcement of labor regulations, including those restrictive

> 10Our conceptualization of the implicit labor tax is similar to that in Hsieh and Klenow (2009).

3
of contract hiring.<sup>11</sup> Contract hiring may be attractive not just because of the high retrenchment costs of regular workers imposed by IDA, but also due to other laws concerning workplace safety regulations, social security taxes and business registration requirements which may add to the effective compliance cost of employing a regular worker. Hence, a perceived relaxation in labor law enforcement may cause firms to switch to contract hiring. Consistent with this idea, we show that the firm level impact of the IDA amendment was stronger in industries inherently more contract labor intensive in India.

Our findings add to the evidence base on the economic impact of labor regulations. As noted, in the case of India, there are many studies examining the impacts of the IDA on firms using some version of a state level labor law index.<sup>12</sup> Some recent studies have focused on the role of contract hiring as a response to the stringency of IDA (Bertrand and Tsivanidis (2017), Chaurey (2015) and Chakraborty, Singh and Soundararajan (2020)). Beyond India, there is a large body of research looking into the impacts of employment protection laws in Europe and the US.<sup>13</sup> In particular, we contribute to the literature which estimates the economic impact of employment protection laws by exploiting specific policy changes within a country. Recent research in this vein exploits the variation in the adoption of wrongful-discharge protection by US states (Autor, Kerr and Kugler 2007), the variation in court judgements on dismissals for economic reasons in Japan (Okudaira, Takizawa and Tsuru 2013) and a change in seniority-based hiring regulations in Sweden (Bjuggren 2018).

In examining the impact of labor laws on the implicit labor tax on firms, our study also contributes to the literature on how cross-country differences in productivity and income are related to the misallocation of resources across firms.<sup>14</sup> Identifying specific sources of firm-level misallocation, particularly those distortions that implicitly tax more productive firms more severely, is an important question in this literature (Restuccia and Rogerson 2017). The size-dependent features of labor laws such as the IDA are a case in point, as they potentially impose higher regulatory costs as firms grow. In this broad context, our paper is related to recent work study-

> 11It was noted in the press that the concurrent changes to the IDA and the CLA sent a confusing signal on the official stance towards permanent versus contractual employment (Sharma 2014).

> 12For example, Besley and Burgess (2004), Ahsan and Pag ́es (2009), Hasan R. and Ramaswamy (2007) and Aghion et al. (2008).

> 13See, for example, Bentolila and Bertola (1999) and Di Tella and MacCulloch (2005), and the survey in Kugler (2007). Recent work examining the use of temporary or informal contracts as a response to employment protection laws includes Hijzen, Mondauto and Scarpetta (2017) and Vallanti and Gianfreda (2021).

> 14See, for example, Hsieh and Klenow (2009) and Hsieh and Klenow (2014).

4
ing the impact of size-dependent labor regulations on firm performance in India (Amirapu and Gechter 2020), France (Garicano, LeLarge and Reenen 2016) and Portugal (Braguinsky, Branstetter and Regateiro 2011).

The rest of the paper is organized as follows. Section 2 describes labor regulation in India and the amendments enacted by Rajasthan. Section 3 explains our methodology. Section 4 presents data and descriptive statistics. Sections 5 and 6 discuss the estimation results, and Section 7 concludes.

# **2 Institutional background**

## **2.1 Labor regulation in India**

Working conditions and employment adjustments in Indian firms are governed by a complex regulatory structure underpinned by multiple laws and varying across government authorities (central and states), establishment sizes, and types of laborers. The labor law that features most prominently in the economic literature is the Industrial Disputes Act, 1947, which governs the resolution of industrial disputes concerning “permanent” (or, “regular”) workers, the hiring and firing of permanent workers and the closure of factories. IDA rules concerning lay-off, retrenchment and closure are particularly contentious. Chapter V-A of the Act regulates lay-offs and closures, with several of its provision applying to establishments with 50 or more regular workers. Workers who have been on the rolls for at least a year are entitled to compensation at 50 percent of their regular wage for each day that they are laid off (up to a maximum of 45 days). Those who are to be retrenched are to be given one month’s notice and are eligible for compensation equal to 15 days’ average pay for each year of completed service. Section V-A also requires 60 days advance notification of closure to the government, with workers affected by the closures to be compensated at the same rate as retrenched workers.<sup>15</sup> In addition to Chapter V-A, Chapter V-B applies to establishment with more than 100 workers and requires government permission for retrenchment, and a 90 day advance notice for closure.<sup>16</sup>

> 15Establishments with fewer than 50 workers are exempted from a few sections of Chapter V-A that require compensation for layoffs, maintenance of muster rolls, and 60 days’notice before closure. They are subject to the same prescribed rates of severance pay in cases of retrenchment or closure (Bhattacharjea 2017).

> 16Chapter V-B originally applied to firms employing 300 or more workers. The threshold was lowered to 100 by an amendment passed in 1982. The penalty for violating the regulations in V-B includes a prison

5
The IDA has been amended in 1982 by the central government and multiple times by state governments. Besley and Burgess (2004) document these amendments and code them as proworker, neutral or pro-employer. Other authors have subsequently developed similar indices by modifying the Besley and Burgess (2004) index or using another codification method.<sup>17</sup> The methodology behind such indices, in particular the interpretation of certain IDA amendments as being pro-worker or pro-employer, has been critiqued by Bhattacharjea (2006).

Another key law is the Factories Act of 1948, which governs conditions of work in formal manufacturing establishments. The Act contains certain requirements to ensure the health and safety of factory workers, including regulations on the hours of work, overtime and annual leave, and female and child labor conditions. It applies to all factories that employ 10 or more regular workers (the relevant threshold for units not using electricity is 20 or more employees).<sup>18</sup> A number of regulatory requirements other than the Factories Act also start binding at the threshold employment sizes of 10 or 20 workers.<sup>19</sup> The growing use of contract workers by Indian manufacturing firms too is notable. A contract worker –as understood in the context of India’s formal sector— is the permanent employee of a staffing agency (or the _contractor_ ) who is hired out to another firm (the _employer_ ) on a temporary basis.

Historically, the regulatory stance towards contractual hiring has not been a permissive one. The 1982 IDA amendment declared the continuing employment of workers on casual or temporary contracts to be an “unfair labor practice” (Mitchell, Mahy and Gahan 2014). The Contract Labor (Regulation and Abolition) Act is applicable to establishments employing at least 20 contractors on any day over the previous 12 months. Employers are required to declare the number of contract workers and what they do. The act is generally restrictive of the use of contract workers in the “core” activities of an establishment; that is, the tasks typically done by permanent workers

> term of up to a year or a fine of 5,000 rupees in the case of illegal closure (or both) and prison term of up to a month and a fine of 1,000 rupees in the case of illegal layoff or retrenchment.

> 17Hasan R. and Ramaswamy (2007), Ahsan and Pag ́es (2009), Gupta, Hasan and Kumar (2009) and OECD (2007).

> 18Similarly, the regulation of smaller manufacturing units, shops, and other types of small workplaces is laid out in the Shops and Commercial Establishments Acts.

> 19They include the Minimum Wages Act 1948 (which sets minimum wages), the Payment of Bonus Act 1965 (which regulates bonus payments) and the Equal Remuneration Act 1976 (which prescribes equal pay for equal work between male and female workers in establishments with 10 or more employees). The Employees’ State Insurance Scheme, the Employees’ Provident Fund and the Payment of Gratuity Act 1972 concern the social security and welfare obligations of employers.

6
in that industry.<sup>20</sup> The CLA also entitles contract workers to minimum wages, workplace health and safety provisions, and social security cover such as Employee Provident Fund benefits. The provision of these minimum benefits is the primary responsibility of the contractor, but needs to be verified by the firm using the contract worker. Firm surveys suggest that the CLA is not wellenforced, with non-adherence to its provisions regarding minimum compensation and restricted use of contract workers for core activities being common (Rajeev (2009) and Singh, Das, Choudhury, Kukreja and Abhishek (2017)). For example, 82% of firms with 0-99 employees and 68% of those with 100-499 employees replied in the affirmative to the question “Do contract workers replace permanent workers?” in a recent survey (Singh et al. (2017)).

# **2.2 Rajasthan’s labor law amendments**

Rajasthan passed several amendments to industrial labor laws in November 2014.<sup>21</sup> Their highlight was a pro-employer amendment to IDA: the employment size threshold above which a factory requires government permission for retrenchment (Chapter V-B) was raised from 100 to 300 workers. Another pro-employer amendment to the IDA made unionization more difficult by mandating that union membership must reach at least 30 percent of the establishment’s total workforce, as opposed to the 15 percent required earlier. It was also mandated that workers who wish to raise an objection with the government regarding their discharge or retrenchment must do so within 3 years of being discharged. There was no time limit earlier.

Two other laws directly related to labor regulation were also amended. First, the Contract Labor (Regulation and Abolition) Act would now apply to establishments with 50 or more contract workers. It used to apply to establishments with 20 or more contract workers. Second, the threshold above which the Factories Act applies was raised from 10 to 20 workers (40 in case of units without power).

> 20Section 10 of the Act gives authority to the government to control the use of contract labor in any establishment. Some state governments have even made amendments to explicitly prohibit the use of contract labor for core activities.

> 21See G.o.Rajasthan (2014c), G.o.Rajasthan (2014a) and G.o.Rajasthan (2014b)

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# **3 Methodology**

## **3.1 Synthetic control case study**

We first employ the synthetic control method for a state-level comparative case study of the impact of Rajasthan’s labor law amendments on the state’s aggregate industrial outcomes. This method is increasingly used to study the aggregate-level impacts of interventions that affect a small number of aggregate entities (in our case, a single state). It entails comparing the evolution of aggregate outcomes of interest in the entity affected by the intervention (the treatment unit) with comparable entities not affected by the intervention (the control).

The synthetic control method uses a systematic, data-driven procedure to select the control group. The idea behind this approach is that often, a weighted combination of potential comparison units is a good control group (Abadie and Gardeazabal (2003); Abadie et al. (2010)).

Suppose there are a total of _J_ + 1 units (such as states) indexed by s. Let _Yst_ be unit _s_ ’s period _t_ outcome in the absence of the intervention. The intervention affects unit _s_ = 1 at a time _T_ 0 _>_ 1. The other units are the potential controls. Suppose that Here, ∆ _t_ is a time-varying factor that affects all units similarly, _Zs_ a vector of observed covariates not affected by the intervention, Λ _t_ a vector of unobserved time-varying common factors whose effect on the outcome depends on unknown unit-specific factors _μs_ , and _est_ an unobserved transitory shocks with zero mean. In order to estimate the impact of the intervention at time _t > T_ 0, we first need to estimate _Y_ 1 _t_ , that is, the counterfactual outcome in the absence of the intervention. The estimated impact will then be the difference between the actual, observed outcome of the treated unit at time _t_ and the counterfactual outcome.

Suppose there exists a _JX_ 1 vector of weights _wj_<sup>_∗_such that</sup> (a) The weighted outcome of the potential controls equals the outcome of the treated unit in all pre-intervention periods, and (b) The weighted value of the covariates (the _Zs_ ) of the potential controls equals the covariate values of the treated unit.

Then, as shown in Abadie et al. (2010), the weighted outcome of the potential control units (using the weights _wJ_<sup>_∗_) in a post-intervention period</sup><sup>_t_will be close to the counterfactual</sup><sup>_Y_1</sup><sup>_t_, pro-</sup> 8
vided that the number of pre-intervention periods is large relative to the scale of the transitory shocks. The intuition behind this result is that if conditions (a) and (b) are true, then it must be that the weighted values of the relevant unobserved characteristics of the control group best resemble those of the treated unit.

In practice, suppose _X_ is a set of variables that includes some of the observed covariates ( _Z_ ) as well as the outcome _Y_ for some of the pre-intervention years. These are the “predictor” variables. The synthetic control weights _wj_<sup>_∗_are selected to minimize the distance between the predictor vari-</sup> able values of the treatment unit (that is, _X_ 1) and the synthetic control (that is, the weighted mean _Xs_ of the control group).<sup>22</sup> We implement the method in Stata using the synth package. The synth package implements the procedures outlined in Abadie and Gardeazabal (2003) and Abadie et al. (2010), and optimizes the choice of weights using a nested procedure.<sup>23</sup> Following the standard practice in synthetic control studies, we also conduct placebo tests to address the uncertainty about how well the synthetic control reflects the counterfactual (Abadie et al. (2010); Abadie et al. (2015)). It would be difficult to argue that the synthetic control estimates truly reflect the impact of the intervention if it is common to obtain estimates of similar or larger magnitudes in placebo treatments.

Note that a significant difference in post-intervention outcome between the treated unit and its synthetic control – as measured by size of the post-intervention Mean Squared Errors (MSE) – would convince us that the intervention had an impact only if the synthetic control matched the treated unit’s pre-intervention outcome closely; that is, if the pre-intervention MSE was low. Hence, it is the ratio of the post and pre-intervention MSEs that matters for inference, with a higher MSE ratio in the true treatment case adding to our confidence in the estimate. The inferential

> 22This distance is typically measured as the squared sum of deviations, wherein the squared difference between the treatment unit and synthetic control value is calculated for every predictor variable and summed up.When calculating this squared sum of deviations, the predictor variables are weighted according to their predictive power on the outcome variables. These predictor variable weights should be chosen so that the resulting synthetic control closely tracks the relevant outcome of the treatment unit in the pretreatment period.

> 23The procedure first calculates starting points for the predictor variable weights using three approaches - a) data-driven regression based method; b) equal weights; and c) weights calculated using Stata’s Maximum Likelihood search procedure. Given a particular set of predictor variable weights, it then calculates the corresponding synthetic control _wj_ weights, and the resulting mean squared prediction error in the outcome variable over the pre-intervention period. It then uses a nested optimization procedure that searches among predictor variable weights (and corresponding _wj_<sup>_∗_weights) for the best fitting convex combination</sup> of the control units. Among the three approaches for selecting a starting point, the approach that gives the best result is then adopted.

9
exercise essentially seeks to confirm that the MSE ratio for the true case is large relative to the distribution of the MSE ratio among the placebos.

We implement the placebo test by sequentially assigning every potential control state to the placebo treatment and verifying whether it is unusual to find MSE ratios as large as Rajasthan’s when the treatment is assigned at random to other states.

# **3.2 Difference-in-differences analysis with firm-level panel data**

In the main empirical analysis presented in this paper, we use firm-level panel data to conduct a difference-in-differences analysis of the impact of the main amendment, the repeal of IDA Chapter V-B for firms with fewer than 300 workers. Since firms with fewer than 100 workers were never subject to Chapter V-B in the first place, the amendment changed firing cost among firms that had between 100 and 300 workers at baseline (that is, the year the amendment was passed). We consider these firms to be our treatment group, and compare the post-treatment change in their outcome with that of firms employing more than 300 workers at baseline. The latter is an appropriate control group as it continued to be subject to IDA Chapter V-B even after the amendment. Moreover, we compare this differential change in the outcomes of the treated and control groups of firms across Rajasthan and other states (that is, we estimate a triple difference). As contract workers are not technically on the payroll of firms under IDA, we define the threshold based on regular workers alone, in line with Chaurey (2015).

The main difference-in-differences specification is as follows: Here, _yit_ is an outcome of interest in firm _i_ and year _t_ . _Postt_ is a dummy for post-treatment years, _Treati_ is a dummy equal to one if firm _i_ had 100-300 regular workers in the baseline year, and _Rajasthani_ is a dummy equal to one if the firm _i_ is located in Rajasthan. The regression includes year-specific dummies _Y eart_ and firm fixed effects _μi_ . The equation is estimated for firms that had 100 or more workers at baseline; hence, firms with more than 300 regular workers at baseline constitute the control group.

The main coefficient of interest is _γ_ , which captures the differential post-treatment change in the outcome of firms with baseline employment between 100-300 (relative to firms with baseline 10
employment above 300) across Rajasthan and other states. The _Postt × Treati_ term controls for contemporaneous shocks to the manufacturing sector that were constant across states but varied systematically across firms with 100-300 workers and 300 plus workers at baseline. The _Postt × Rajasthani_ term controls for shocks to the manufacturing sector that were common to firms of different sizes at baseline but varied across Rajasthan and other states.

We report standard errors clustered at the firm level to account for serial correlation in firm level shocks.

# **3.3 Robustness checks**

A key assumption behind the difference-in-differences specification described in equation 3 is that there was no pre-intervention trend in the outcome that varied by firm size group and by state. We examine this assumption through a more flexible event-study specification: This specification estimates year-specific coefficients (the _γt_ s) on the key interaction term _Treati× Rajasthani_ . The omitted year dummy corresponds to the baseline year. Hence, the _γt_ s measure differences relative to the baseline year. A systematic pattern in the _γ_ s for the pre-treatment years would indicate that the assumption of no differential prior trend in the outcome is not valid.

The event study specification also allows us to examine the dynamic effects of the intervention, by examining how the _γ_ s evolve in the post-treatment years. That being said, having only three years of post-intervention data, our study has limited power to discern dynamic effects, and the basic difference-in-differences regression (3) remains our preferred specification.

Another concern is whether firms from all major Indian states excluding Rajasthan are a good control group. We have no reason to believe otherwise, but in a sense this choice is arbitrary. As noted in Section 3.1, when estimating impacts on aggregate outcomes in state level analysis, the synthetic control method offers a systematic and data-driven approach for selecting the control group of states. Lacking such a method for firm-level analysis, our approach is to check if the results are robust to varying the states from which firms in the control group are drawn. We 11
consider two alternative control groups: firms from states at a similar level of GDP per capita to Rajasthan (Andhra Pradesh, Chatisgarh, Jharkahnd, Madhya Pradesh and West Bengal)<sup>24</sup> and states that neighbour Rajasthan (Gujarat, Haryana, Madhya Pradesh, Punjab and Uttar Pradesh).

Strategic misreporting of employment levels too is a concern in this setting (Amirapu and Gechter 2020). In particular, the concern is that firms that stood to benefit substantially from the anticipated repeal of Chapter VB but were above the 300 worker size threshold at baseline might have misreported their employment as being below 300 at baseline. This could exaggerate the estimated impact of the amendment. We redefine the treatment status based on the average employment level in the three most recent pre-treatment years to address this particular concern. This approach assumes that strategic misreporting two to three years in advance of the amendment was unlikely.<sup>25</sup>

# **3.4 Estimating the implicit tax on labor**

A key outcome of interest in this study is impact of the amendments on the hidden labor costs imposed on firms by Indian labor laws. As in Hsieh and Klenow (2009), we characterize this cost as an implicit tax that adds to the variable cost of labor. We estimate the impact of the amendments on this implicit tax using a method based on the firm’s cost minimization approach (Chaurey et al. 2019).<sup>26</sup> An advantage of this method is that it does not require us to specify the structure of market demand for the firm’s output, nor does it require us to estimate the coefficients of a specific production function.

Consider a firm i’s production function _Q_ ( _L, M_ ) with two variable factors of production, labor _L_ and materials _M_ . The firms cost minimization problem in period _t_ is as follows: Here _Qit_ is the level of production that the firm is trying to minimize costs for. _Pit_<sup>_L_and</sup><sup>_P M_</sup> _it_<sup>are</sup> the price of labor and material, respectively. We assume that these input prices can vary across

> 24These states were shortlisted based on average GDP per capita from 2012 to 2015

> 25Note that there is a trade off involved in such redefinition of treatment: while reducing the potential bias from strategic under-reporting of employment at baseline, it also reduces the accuracy of the assignment to treatment and control.

> 26The method developed in Chaurey et al. (2019) builds on the cost minimization approach to measuring firm-level price markups used in De Loecker and Warzynski (2012).

12
firms, but cannot be affected by the firm (that is, the firm acts as a price taker in factor markets). _τit_<sup>_L_and</sup><sup>_τ M_</sup> _it_<sup>are the implicit taxes on labor and materials, respectively.They are not paid explicitly</sup> (that is, not included in the firm’s reported expenditure on the factor).

Here, _ρit_ is the firm’s output price markup. _θit_<sup>_L_and</sup><sup>_θ_</sup> _it_<sup>_M_are the elasticities of output with respect</sup> to labor and material, respectively, and depend on the production function. _κ_<sup>_L_</sup> _it_<sup>and</sup><sup>_κM_</sup> _it_<sup>arethe</sup> expenditures on labor and materials, respectively, divided by the firm’s revenue.

Dividing the two first order conditions, we see that the optimal ratio of input expenditures is inversely proportional to the implicit input taxes: Normalizing the implicit tax on materials to 1 - in other words, redefining _τit_<sup>_L_astherelative</sup> implicit tax on labor - and taking logarithms, we see that: Suppose that the production function of firm _i_ is of the Cobb-Douglas type, and does not vary _<u>it</u>_ over time in study period. Then the input elasticity term _log_ ( _θ_<sup>_θ_</sup> _it_<sup>_ML_) in equation 7 is time-invariant,</sup> and within-firm changes in the logarithm of the relative input expenditure shares over time reflect changes in the logarithm of the implicit labor tax. The assumption that the firm’s technology is constant is reasonable given the short time frame of the firm level analysis. Hence, we can estimate changes in the implicit labor tax by using the log of the input expenditure shares as an outcome variable in the difference-in-differences panel regressions with firm fixed effects (which subsume the constant input elasticity term). When implementing this method, we use the log of expenditure on raw materials relative to labor.

13
# **4 Data and descriptive statistics**

The main data source for this paper is India’s Annual Survey of Industries (ASI), a survey of the formal manufacturing sector conducted by India’s Ministry of Statistics and Program Implementation (MoSPI). The sample frame of the ASI consists of all industrial units (“factories”) registered under Sections 2(m)(i) and 2(m)(ii) of the Factories Act, 1948. This includes all factories employing 10 or more workers if they use power, and those with 20 or more workers if they do not. The ASI has two parts: a census of all factories employing 100 workers or more and a survey that randomly samples about a quarter of all other registered factories.

The ASI collects annual data for the most recent accounting year. For example, ASI 2015 collected data on the accounting year ending March 2015. Since the Rajasthan amendments were passed in November 2014, we consider the accounting year ending in March 2015 as the baseline year of the policy change studied in this paper, and hereafter refer to it as 2015. Thus, 2016 is the first post-treatment year of our study.

## **4.1 State-level panel data for synthetic control analysis**

We use annual state level data on the formal manufacturing sector for the years 1980-2018 in the synthetic control analysis. The data set is a compilation of state level ASI summary data published by the MoSPI.<sup>27</sup> The ASI is stratified by state _X_ 3-digit industry group, and state and industry level aggregates can be estimated by weighting the factory level data by the inverse of the sampling probabilities. The compiled data set includes estimates of total output (revenue), employment and fixed capital by state which match the officially published numbers.

Since officially published state-level ASI summary statistics do not include data on contract workers, we use unit level ASI data from 2001-2018 to estimate state level contract employment.<sup>28</sup> We drop the urban state of Delhi, union territories and small states with a population less than 10 million in 2001 (Jammu and Kashmir, Himachal Pradesh and north-eastern states expect for Assam) from the control donor pool of the synthetic control analysis. Hence, besides Rajasthan, the panel includes fourteen donor pool states : Andhra Pradesh, Bihar, Karnataka, Kerala, Madhya Pradesh, Maharashtra, Orissa, Punjab, Tamil Nadu, Uttar Pradesh, West Bengal, Assam, Gujarat

> 27The state-industry data on factories from 1980-1997 were used by Aghion et al. (2008). We are grateful to the authors and the American Economic Review for making these data publicly available.

> 28We verify that the total state output and employment estimates constructed by us from unit-level ASI data match the officially published numbers.

14
and Haryana.<sup>29</sup> The baseline predictor attributes used to determine the synthetic control includes variables such as the share of urban population, the literacy rate, the number of males, females, number of workers, number of main and marginal workers, cultivators, agricultural laborers and percentage of Scheduled Caste and Scheduled Tribes, reflecting key structural features of Indian states. These variables are available from the 2001 Census. The predictor variables also include lagged values of the outcome variable for three years: 2014, 2009 and 2004.

# **4.2 State-level descriptive statistics**

Tables 10 in the Appendix summarizes the key outcome variables of the ASI state level panel data set while Table 11 summarizes the predictor variables.

Figure 1 presents trends in state-level nominal output and employment in the formal manufacturing sector during 2001 and 2016, comparing Rajasthan to the average of other states in donor pool. Rajasthan has a smaller formal manufacturing sector that the average state. Notably, Rajasthan’s output trend has differed from that of the average other state. Between 2001 and 2010, Rajasthan grew slower than other states, with the ratio of their outputs falling from approximately 0.6 to 0.5. This relative trend appears to have reversed later, with the ratio of output in Rajasthan and the average other state climbing back to 0.6 in 2015. This differential aggregate trend underscores the potential gains from a data driven approach to selecting the control group.

> 29Three new states – Uttarakhand, Jharkhand and Chattisgarh- were carved out of the states of Uttar Pradesh, Bihar and Madhya Pradesh, respectively, in 2001. The state of Telangana was carved out of Andhra Pradesh in 2014. Our state level data set features the undivided versions of these states to maintain consistency in state definitions.

15
<!-- Start of picture text --> +<br>°<br>3<br>:FE<br>§<br>.<br>o<br>s<br>2000 2005 2010 2015<br>Year<br>——— Rajasthan ————Other States (Avg)<br><!-- End of picture text --> <!-- Start of picture text --> 100%<br>75%<br>= 300+<br>50% m 150-300<br>100-150<br>650-100<br>25% w<50<br>0%<br>Output Employment Contract Employment<br><!-- End of picture text --> <!-- Start of picture text --> :<br>8<br>28<br>5<br>ss<br>:<br>r=]<br>:<br>ow 2000 2005 2010 2015 2020<br>Year<br>——— Rajasthan ————Other States (Avg)<br><!-- End of picture text --> <!-- Start of picture text --> 100%<br>75%<br>300+<br>50% w 150-300<br>w 100-150<br>50-100<br>25% <0<br>0%<br>Output Employment Contract Employment<br><!-- End of picture text -->
# **4.3 Firm-level panel data**

We construct a firm-level panel dataset using the annual ASI data. We use firm identifiers to track firms over the years 2010-2018 and limit the sectors to manufacturing- related sectors and omit agriculture and other primary activities. As mentioned earlier, the ASI survey does not cover all firms every year and chooses a sample of small firms to be covered. Our study, however, focuses on all firms with at least 100 workers. As the ASI survey is supposed cover all such large firms in every round (as part of the “census” section of the ASI), we are less likely to lose out on firm observations because of sampling. In addition, we do not lose out on a lot of manufacturing activity because as discussed, this subset of large firms accounts for most of formal manufacturing activity.

The dataset includes information on the 3-digit industry group and the state in which the firm is located. It also includes information on output, inputs and employment. On employment, it covers labor involved in production as well as the split of workers into contract and permanent categories. For each of the labor categories, there is also information on the total wages paid out. With regard to inputs, the dataset covers expenditure on the fixed capital stock as well as variable domestic and directly imported inputs (that is, materials) sourced by the firm in the last fiscal year. We sum up the latter two expenditures to get a measure of the firm’s total expenditure on variable material inputs.

Similar to the case of the state- level panel, this dataset also drops all small states and union territories. In addition, we have to drop firms that were in the new state of Telangana as it was not possible to track the firms back in the period before the split. The dataset does not consider those firm observations that do not report any labor information. All outcomes are winsorized at the 1/99 level by year.

# **4.4 Firm-level descriptive statistics**

Table 12 describes the outcome variables used in the firm (factory) level panel analysis. The panel analysis is limited to firms with 100+ workers at baseline, with the treatment group covering firms with 100-300 workers and the control group covering firms with more than 300 workers. Given that the treatment and control groups are defined based on size, one would expect them to be different on this dimension. As the table suggests, the typical firm in the treatment group has fewer employees compared to a typical control firm and this difference is statistically significant 17
for both Rajasthan and Rest of India.

The share of contract labor is about 6-7 percentage points lower in larger control firms, across Rajasthan and the other states. There is, however, no statistically significant difference between the treatment and control group as far as the share of contract labor in total labor is concerned. The estimated log expenditure on material inputs (relative to labor) is also not statistically different across both treatment and control, for Rajasthan as well as other states.<sup>30</sup>

# **5 Estimation results: State-level synthetic control analysis**

In this section, we present the results of the analysis using the 1980-2018 long panel, looking at aggregate output and employment in the formal manufacturing sector. We first consider the impact on total employment. Figure 3 presents the evolution of aggregate employment in Rajasthan and its synthetic control, and the MSE ratios from the placebo estimations. Table 13 in the appendix presents the balance between Rajasthan and the synthetic control for employment, and the weights on the control states in the synthetic control.

The synthetic control tracks Rajasthan closely between 1990 and 2014, adding to our confidence in its ability to replicate what would happen to Rajasthan absent the treatment (Panel A). But there is no sizable widening of the gap in total employment levels between Rajasthan and the synthetic control in the three post-treatment years. The average post-treatment gap in employment between Rajasthan and the synthetic control is 1 percent.

Panel B presents the key results of the placebo tests. Recall that inference testing in synthetic control is based on conducting placebo estimations on control units and examining the distribution of the ratio of the post and pre-treatment MSEs for the placebos. The purpose of this exercise is to assess the likelihood of obtaining a post-treatment gap (relative to the pre-treatment gap) as large as that observed in the treatment unit through sheer chance. In this case, the placebo tests indicate that Rajasthan’s MSE ratio is not unusually large compared to the ratios obtained when treatment is assigned randomly. Thus, the results suggest that the amendments did not have a significant impact on aggregate employment.

> 30As described in the previous section, this variable represents the relative adjustment cost of labor after we account for firm- specific fixed effects in the estimation

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<!-- Start of picture text --> $s<br>° Effect :: 1 perc<br>8<br>s~<br>o<br>"oa a<br>Es<br>22 *<br>5 p<br>3<br>a oad<br>o |rett rhe —<br>8<br>1980 1990 2000 2010 2020<br>Yeear<br>——— Rajasthan -~~-~~ Synthetic Control<br>Note: Treatment Effect = Post - Avg (Treatment - Control)! Pra- Avg (Control)<br><!-- End of picture text -->

<!-- Start of picture text --> Post/ Pre- 2015 Mean Square Prediction Error<br>Kerala<br>Punjab<br>Uttar Pradesh<br>Tamil Nadu<br>Andhra Pradesh<br>Bihar<br>West Bengal<br>Karnataka<br>Madhya Pradesh<br>Orissa<br>Rajasthan<br>Maharashtra<br>0 1 2 3 4 5<br><!-- End of picture text -->
<!-- Start of picture text --> = Effect : 21.7 pere<br>r<br>= . J<br>Sai i<br>=a<br>&<br>Ss<br>$5 .<br>or rr,<br>we<br>a<br>1980 1990 2000 2010 2020<br>Year<br>——— Rajasthan -—~~-~~ Synthetic Control<br>Note: Treatment Effect = Post -.Avg (Treatment-Control Pra- Avg (Control)<br><!-- End of picture text --> <!-- Start of picture text --> Post/ Pre- 2015 Mean Square Prediction Error<br>Rajasthan<br>Orissa<br>Tamil Nadu<br>Punjab<br>Bihar<br>Uttar Pradesh<br>West Bengal<br>Andhra Pradesh<br>Madhya Pradesh<br>Kamataka<br>Maharashtra<br>Kerala<br>Qo 2 4 6 8 10<br><!-- End of picture text -->
<!-- Start of picture text --> States with +ve weight in original synthetic control omitted one by one<br>Uttar Pradesh i<br>sihar TT 7s<br>Gujarat ER 29<br>-10 5 0 5 10 15 20<br><!-- End of picture text -->
Finally, column 6 in Table 1 presents the difference-in-differences estimates of the impact of the treatment on the implicit regulatory labor tax on firms. As discussed in Section 3.4, we conceptualize the regulatory burden associated with permanent employees as an implicit variable labor cost. Within-firm changes in this hidden cost can be backed out using the firm’s cost minimization problem; they are proportional to changes in the ratio of expenditures on labor and materials. The estimated change in the log of the implicit labor cost is -0.13, significant at the 10 percent level. This implies that the implicit labor cost fell by approximately 14 percent.

Table 2 presents the estimated impacts on the log of output, fixed capital, value added and value adder per worker. The results indicate that the repeal of IDA Chapter V-B did not have a detectable affect on output, investment and labor productivity in the treated firms.<sup>33</sup> Table 1: Firm Level Panel DiD on Employment Outcomes

||(1)<br>Log<br>total workers|(2)<br>Log<br>regular workers|(3)<br>Log<br>contract workers|(4)<br>Share of<br>contract workers|(5)<br>Likelihood of<br>usinganycontract work|(6)<br>Implicit cost<br>of Labor|
|---|---|---|---|---|---|---|
|RJ * Treatment L * Post|0.031|-0.177*|0.807***|0.098***|0.140***|-0.136*|
||(0.065)|(0.101)|(0.241)|(0.028)|(0.050)|(0.075)|
|Treatment L * Post|-0.044***|-0.055***|-0.045|0.004|-0.004|0.022*|
||(0.011)|(0.014)|(0.039)|(0.004)|(0.008)|(0.012)|
|RJ * Post|-0.001|0.069|-0.278|-0.019|-0.048|0.048|
||(0.054)|(0.079)|(0.194)|(0.021)|(0.040)|(0.060)|
|Observations|66,909|66,909|66,909|66,909|66,909|66,909|
|R-squared|0.024|0.023|0.008|0.006|0.005|0.083|
|Number of fact<br>~~n~~um|10,470|10,470|10,470|10,470|10,470|10,470|
|Firm FEs|Y|Y|Y|Y|Y|Y|
|Year Dummies|Y|Y|Y|Y|Y|Y|

Note: Sample restricted to firms with more than 100 workers. Treatment refers to firms with 100-300 workers. All dependant outcome variables represented in log forms here have been assigned an underlying value of 1 when they take a value of zero. Share of contract workers is defined as the share of contract worker in total worker hours used by the firm for that year. Implicit cost is defined using the expenditure on all raw materials as a base. Standard errors in parentheses, clustered at the firm level. *** p _<_ 0.01, ** p _<_ 0.05, * p _<_ 0.1.)

# **6.2 Robustness analysis**

Tables 3, 4, 5 and 6 present some robustness checks on the key panel results regarding employment. In Table 3, we include industry-year dummies to control for differential shocks or trends by industry. This may matter, for example, if Rajasthan’s industrial composition is tilted towards industries in which medium-size firms are replacing permanent workers with contract workers

> 33Instead of taking logs, we use the inverse hyperbolic sine (arcsine) transformation of value added as this variable can have negative values in the data. The inverse hyperbolic sine transformation is similar to the logarithmic transformation and has the same interpretation, but has the advantage that it can also be applied to zero and negative values.

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Table 2: DiD on Out ut and Value Added <u>p</u>

|VARIABLES|(1)<br>Log1 Output|(2)<br>Log1 Fix Cap|(3)<br>Arcsin VA|(4)<br>Arcsin VApl|
|---|---|---|---|---|
|RJ * Treatment L * Post|-0.073<br>(0.072)|-0.051<br>(0.065)|0.060<br>(0.470)|0.008<br>(0.333)|
|Observations|66,909|66,907|66,909|66,909|
|R-squared|0.128|0.076|0.001|0.002|
|Number of fact<br>~~n~~um|10,470|10,470|10,470|10,470|
|Firm FEs|Y|Y|Y|Y|
|Year Dummies|Y|Y|Y|Y|

Note: Sample restricted to firms with more than 100 workers. Treatment refers to firms with 100-300 workers. All dependant outcome variables represented in log forms here have been assigned an underlying value of 1 when they take a value of zero. Share of contract workers is defined as the share of contract worker in total worker hours used by the firm for that year. Implicit cost is defined using the expenditure on all raw materials as a base. Standard errors in parentheses, clustered at the firm level. *** p _<_ 0.01, ** p _<_ 0.05, * p _<_ 0.1.) at a faster pace than in the average industry. The results are robust to including industry-year dummies. Next, to address the concern that firms that stood to benefit substantially from the anticipated repeal of Chapter VB but were above the 300 worker size threshold at baseline might have under-reported their employment as being below 300 in 2015, Table 4 presents the results obtained when we redefine the treatment status based on the average employment level during 2013-2015. The logic behind this is that firms would have little reason to misreport their size two to three years in advance of the amendment, and therefore, redefining treatment based on the average employment in the three years preceding the amendment should reduce the potential bias from strategic misreporting. The results are generally comparable to the baseline specification results.<sup>34</sup> The next set of robustness checks concern the choice of firms from all major Indian states (other than Rajasthan) as the counterfactual in our main specification. We test for the sensitivity of the key results to this choice by considering two alternative counterfactual sets of states: only those neighboring Rajasthan (in Table 5) and only those with per capita GDP similar to Rajasthan (in Table 6). The main results are robust to these changes.

Next, we present the estimation results of the event-study difference-in-differences specification described in equation 3 in Figure 6. The results confirm that there were no systematic pre-trends in the outcomes that could have biased the baseline difference-in-differences estimates.

> 34Some firms appear in the panel only once during 2013-2015. To check that such firms are not driving the results, we have also considered redefining the treatment based on the average employment of the nearest three pre-2015 years of data available since 2010. The results of this redefinition are comparable to the baseline results.

23
Table 3: DiD with Industry*Year Dummies

||(1)<br>Log<br>total workers|(2)<br>Log<br>regular workers|(3)<br>Log<br>contract workers|(4)<br>Share of<br>contract workers|(5)<br>Likelihood of<br>usinganycontract work|(6)<br>Implicit cost<br>of Labor|
|---|---|---|---|---|---|---|
|RJ * Treatment L * Post|0.001|-0.202**|0.726***|0.093***|0.126**|-0.127*|
||(0.065)|(0.100)|(0.239)|(0.027)|(0.049)|(0.076)|
|Observations|66,909|66,909|66,909|66,909|66,909|66,909|
|R-squared|0.037|0.033|0.019|0.017|0.013|0.094|
|Number of fact<br>~~n~~um|10,470|10,470|10,470|10,470|10,470|10,470|
|Firm FEs|Y|Y|Y|Y|Y|Y|
|Year Dummies|Y|Y|Y|Y|Y|Y|
|Industry- Year Dummies|Y|Y|Y|Y|Y|Y|

Note: Sample restricted to firms with more than 100 workers. Treatment refers to firms with 100-300 workers. All dependant outcome variables represented in log forms here have been assigned an underlying value of 1 when they take a value of zero. Share of contract workers is defined as the share of contract worker in total worker hours used by the firm for that year. Implicit cost is defined using the expenditure on all raw materials as a base. Standard errors in parentheses, clustered at the firm level. *** p _<_ 0.01, ** p _<_ 0.05, * p _<_ 0.1.) Table 4: DiD using 2013-2015 average employment to define treatment group

||(1)<br>Log<br>total workers|(2)<br>Log<br>regular workers|(3)<br>Log<br>contract workers|(4)<br>Share of<br>contract workers|(5)<br>Likelihood of<br>usinganycontract work|(6)<br>Implicit cost<br>of Labor|
|---|---|---|---|---|---|---|
|RJ * Treatment Post2013 * Post|0.014<br>(0.065)|-0.166<br>(0.104)|0.649***<br>(0.237)|0.084***<br>(0.027)|0.122**<br>(0.049)|-0.152**<br>(0.071)|
|Observations|66,099|66,099|66,099|66,099|66,099|66,099|
|R-squared|0.018|0.017|0.009|0.010|0.006|0.076|
|Number of fact<br>~~n~~um|9,236|9,236|9,236|9,236|9,236|9,236|
|Firm FEs|Y|Y|Y|Y|Y|Y|
|Year Dummies|Y|Y|Y|Y|Y|Y|

Note: Sample restricted to firms with more than 100 workers. Treatment refers to firms with 100-300 workers. All dependant outcome variables represented in log forms here have been assigned an underlying value of 1 when they take a value of zero. Share of contract workers is defined as the share of contract worker in total worker hours used by the firm for that year. Implicit cost is defined using the expenditure on all raw materials as a base. Standard errors in parentheses, clustered at the firm level. *** p _<_ 0.01, ** p _<_ 0.05, * p _<_ 0.1.

Table 5: DiD with alternate counterfactual: Nei hbor States <u>g</u>

||(1)<br>Log<br>total workers|(2)<br>Log<br>regular workers|(3)<br>Log<br>contract workers|(4)<br>Share of<br>contract workers|(5)<br>Likelihood of<br>usinganycontract work|(6)<br>Implicit cost<br>of Labor|
|---|---|---|---|---|---|---|
|RJ * Treatment L * Post|0.025|-0.156|0.727***|0.094***|0.127**|-0.136*|
||(0.067)|(0.103)|(0.248)|(0.029)|(0.051)|(0.077)|
|Observations|23,174|23,174|23,174|23,174|23,174|23,174|
|R-squared|0.023|0.022|0.009|0.010|0.005|0.109|
|Number of fact<br>~~n~~um|3,329|3,329|3,329|3,329|3,329|3,329|
|Firm FEs|Y|Y|Y|Y|Y|Y|
|Year Dummies|Y|Y|Y|Y|Y|Y|

Note: Sample restricted to firms with more than 100 workers. Treatment refers to firms with 100-300 workers. The states that neighbour Rajasthan include Gujarat, Haryana, Madhya Pradesh, Punjab and Uttar Pradesh. All dependant outcome variables represented in log forms here have been assigned an underlying value of 1 when they take a value of zero. Share of contract workers is defined as the share of contract worker in total worker hours used by the firm for that year. Implicit cost is defined using the expenditure on all raw materials as a base. Standard errors in parentheses, clustered at the firm level. *** p _<_ 0.01, ** p _<_ 0.05, * p _<_ 0.1.

24
Table 6: DiD with alternate counterfactual: States with similar income

||(1)<br>Log<br>total workers|(2)<br>Log<br>regular workers|(3)<br>Log<br>contract workers|(4)<br>Share of<br>contract workers|(5)<br>Likelihood of<br>usinganycontract work|(6)<br>Implicit cost<br>of Labor|
|---|---|---|---|---|---|---|
|RJ * Treatment L * Post|0.041|-0.146|0.790***|0.094***|0.137**|-0.136*|
||(0.071)|(0.108)|(0.260)|(0.030)|(0.053)|(0.081)|
|Observations|12,707|12,707|12,707|12,707|12,707|12,707|
|R-squared|0.016|0.020|0.011|0.014|0.007|0.072|
|Number of fact<br>~~n~~um|2,028|2,028|2,028|2,028|2,028|2,028|
|Firm FEs|Y|Y|Y|Y|Y|Y|
|Year Dummies|Y|Y|Y|Y|Y|Y|

Note: Sample restricted to firms with more than 100 workers. Treatment refers to firms with 100-300 workers. The states having a similar level of GDP per capita to Rajasthan from 2012 - 2015 include Andhra Pradesh, Chatisgarh, Jharkahnd, Madhya Pradesh and West Bengal. All dependant outcome variables represented in log forms here have been assigned an underlying value of 1 when they take a value of zero. Share of contract workers is defined as the share of contract worker in total worker hours used by the firm for that year. Implicit cost is defined using the expenditure on all raw materials as a base. Standard errors in parentheses, clustered at the firm level. *** p _<_ 0.01, ** p _<_ 0.05, * p _<_ 0.1.) Moreover, they indicate that the estimated impacts on contract and permanent employment are not driven by any single post-treatment year. They appear to have persisted at the same level up to three years after the amendment. This suggests that firms made a one-time adjustment to their contract to permanent worker ratio after the amendment was passed.

# **6.3 Why did firms increase contract hiring? Some further analysis**

Besides repealing IDA Chapter V-B among firms with 100-300 workers, Rajasthan also eased the contract labor regulations applying to firms with 20-50 contract workers by exempting them from the CLA.<sup>35</sup> It could be that the switch towards contract workers observed in treated firms is not due to IDA amendment but instead, a result of the CLA Amendment. To test this alternative explanation, we split the IDA treatment group (firms with 100 to 300 workers) into two subgroups based on whether total contract worker employment at baseline was above or below 50. If our results reflect the CLA amendment, then we expect the estimated impacts to be stronger in those treated firms that also became exempt from the CLA in 2105: that is, those with fewer than 50 contract workers at baseline. The results, presented in Table 7, do not support this alternative explanation. In contrast, they suggest that the proportionate increase in contractual employment was larger in treatment firms with more than 50 contract workers at baseline. For example, the point estimate of the percentage increase in contract employment in treatment firms with more than 50 contract employees at baseline is more than twice that in treatment firms with fewer than

> 35Firms with fewer than 20 contract workers were already exempt from the CLA

25
<!-- Start of picture text --> Triple Diff. Estimates for Log1 cont work<br>-<br>o7-f---------4-------- —- -@ - an<br>9~ |<br>a<br>&RS £xs &xv &A &ab &xO &xo &xi &3<br>Ccoetcent on Rajasthan“Treat"Year with frm FES & 100o 900 as treatment& 900 plus as control<br><!-- End of picture text -->

<!-- Start of picture text --> Triple Diff. Estimates for Share - cont<br>o+- !<br>v . . ----@----<br>Pa |<br>&RS £xs &xv &A &ab &xO &xo &xi &3<br>Ccoetcent on Rajasthan“Treat"Year with frm FES & 100o 900 as treatment& 900 plus as control<br><!-- End of picture text -->

<!-- Start of picture text --> Triple Diff. Estimates for Log1 perm work<br>*<br>“0<br>Ofer ro gp<br>s<br>+<br>&sO &xs &NZ &2 &ab &x &xo &x\ &9<br>Ccoetcient on Rajesthan"Treat"Year wih fim FES & 100 10900as treatment & 300 plus as contol<br><!-- End of picture text --> <!-- Start of picture text --> Triple Diff. Estimates for Usage - cont<br>SPT rn a 7<br>I<br>f<br>2<br>&sO &xs &NZ &2 &ab &x &xo &x\ &9<br>Ccoetcient on Rajesthan"Treat"Year wih fim FES & 100 10900as treatment & 300 plus as contol<br><!-- End of picture text -->
Table 7: DiD with treatment group split by contract labor employment above and below 50

||(1)<br>Log<br>total workers|(2)<br>Log<br>regular workers|(3)<br>Log<br>contract workers|(4)<br>Share of<br>contract workers|(5)<br>Likelihood of<br>usinganycontract work|(6)<br>Implicit cost<br>of Labor|
|---|---|---|---|---|---|---|
|RJ * Treatment L (_<_50 cont) * Post|0.061|-0.072|0.534*|0.059*|0.084|-0.146*|
||(0.071)|(0.116)|(0.278)|(0.033)|(0.060)|(0.081)|
|RJ * Treatment L (51+ cont) * Post|-0.018|-0.338***|1.221***|0.157***|0.224***|-0.120|
||(0.081)|(0.121)|(0.262)|(0.032)|(0.050)|(0.100)|
|Observations|66,909|66,909|66,909|66,909|66,909|66,909|
|R-squared|0.027|0.023|0.010|0.008|0.005|0.083|
|Number of fact<br>~~n~~um|10,470|10,470|10,470|10,470|10,470|10,470|
|Firm FEs|Y|Y|Y|Y|Y|Y|
|Year Dummies|Y|Y|Y|Y|Y|Y|
|F-test|1.118|4.534|6.648|7.690|6.692|0.0711|
|Prob¿F|0.290|0.0332|0.00994|0.00556|0.00970|0.790|

Note: Sample restricted to firms with more than 100 workers. Treatment refers to firms with 100-300 workers. All dependant outcome variables represented in log forms here have been assigned an underlying value of 1 when they take a value of zero. Share of contract workers is defined as the share of contract worker in total worker hours used by the firm for that year. Implicit cost is defined using the expenditure on all raw materials as a base. Standard errors in parentheses, clustered at the firm level. *** p _<_ 0.01, ** p _<_ 0.05, * p _<_ 0.1.) 5). This adds to the evidence suggesting that the estimated treatment effects are not ascribable to the CLA amendment.

Table 8: DiD: Im licit Costs S lit b Contract and Permanent Workers <u>p p y</u>

|VARIABLES|(1)<br>All frms<br>Implicit cost<br>contract workers|(2)<br>All frms<br>Implicit cost<br>regular workers|(3)<br>contract_≤_50<br>Implicit cost<br>contract workers|(4)<br>contract_≤_50<br>Implicit cost<br>regular workers|(5)<br>contract_>_50<br>Implicit cost<br>contract workers|(6)<br>contract_>_50<br>Implicit cost<br>regular workers|
|---|---|---|---|---|---|---|
|RJ * Treatment L * Post|-2.348***|0.131|-1.876|0.368|-3.275***|-0.032|
||(0.816)|(0.221)|(1.335)|(0.366)|(0.906)|(0.229)|
|Observations|66,909|66,909|41,231|41,231|25,678|25,678|
|R-squared|0.005|0.022|0.023|0.031|0.075|0.014|
|Number of fact<br>~~n~~um|10,470|10,470|6,816|6,816|3,654|3,654|
|Firm FEs|Y|Y|Y|Y|Y|Y|
|Year Dummies|Y|Y|Y|Y|Y|Y|

Note: Sample restricted to firms with more than 100 workers. Treatment refers to firms with 100-300 workers. All dependent outcome variables represented in log forms here have been assigned an underlying value of 1 when they take a value of zero. Share of contract workers is defined as the share of contract worker in total worker hours used by the firm for that year. Implicit cost is defined using the expenditure on all raw materials as a base. Standard errors in parentheses, clustered at the firm level. *** p _<_ 0.01, ** p _<_ 0.05, * p _<_ 0.1.) Finally, we present analysis suggesting that the strength of the impact of the IDA amendment is linked to the inherent technological viability of contract labor in firms. Following the method used in Rajan and Zingales (1998), we proxy for the inherent viability of (or dependence on) contract labor in firms by using national averages of contract labor intensity by industry. Specifically, we measure the national average firm level share of contract labor in total employment in each industry, and classify industries with above (resp., below) median contract labor share as high (resp., low) contract labor intensity industries. Our assumption is that industries with higher 27
observed contract labor intensity are those in which it is easier to use contract labor for core, industry-specific tasks. We then examine if the impact of the IDA amendment was larger in the high contract intensity group by including an interaction of a dummy for high contract intensity with the _RJ ∗ Treatment ∗ Post_ term in the difference in differences regression.<sup>36</sup> The results, presented in Table 9, show that one of the two main impacts of the IDA amendment, the switch towards contract labor, was felt more strongly in industries with inherently higher contract labor intensity in India. Specifically, the treatment impacts on contract and permanent employment, share of contract workers and incidence of contract workers (columns 2-5) were all significantly higher in the high contract labor intensity group. This suggests that the amendment may have eased binding regulatory constraints on contract labor hiring in firms with the potential to replace permanent workers with contract workers in core tasks.

Table 9: Pre-post DiD: Relative impact by Contract Labor Intensity

|VARIABLES|(1)<br>Log1 work|(2)<br>Log1perm work|(3)<br>Log1 cont work|(4)<br>Share - cont|(5)<br>Usage - cont|(6)<br>Implicit cost work(All inp)|
|---|---|---|---|---|---|---|
|RJ * Treatment L3 * Post * High Contract Intensity|0.177***|-0.363***|1.323***|0.180***|0.247***|0.019|
||(0.067)|(0.123)|(0.270)|(0.034)|(0.059)|(0.087)|
|RJ * Treatment L * Post|-0.075|0.041|0.014|-0.010|-0.008|-0.147*|
||(0.075)|(0.124)|(0.294)|(0.033)|(0.063)|(0.087)|
|Observations|66,909|66,909|66,909|66,909|66,909|66,909|
|R-squared|0.025|0.024|0.010|0.008|0.006|0.083|
|Number of fact<br>num|10,470|10,470|10,470|10,470|10,470|10,470|
|Firm FEs|Y|Y|Y|Y|Y|Y|
|Year Dummies|Y|Y|Y|Y|Y|Y|

Note: Sample restricted to firms with more than 100 workers. Treatment refers to firms with 100-300 workers. Firms are defined to have a high contract intensity if the average share of contract workers used in the corresponding sector at the national level before 2015 was more than 0.35. All dependant outcome variables represented in log forms here have been assigned an underlying value of 1 when they take a value of zero. Share of contract workers is defined as the share of contract worker in total worker hours used by the firm for that year. Implicit cost is defined using the expenditure on all raw materials as a base. Standard errors in parentheses, clustered at the firm level. *** p _<_ 0.01, ** p _<_ 0.05, * p _<_ 0.1.)

> 36This is a quadruple difference term, with all lower degree interactions also included but not shown for the sake of concision.

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# **7 Conclusion**

Exploiting a natural experiment generated by a major policy change in Rajasthan, our paper provides new evidence on long debated questions about the impact of employment protection laws. Our results suggest that reforming extreme employment protection provisions can reduce the implicit regulatory tax on labor in firms. Given that such provisions often tend to be size-dependent, they could be a key part of the explanation behind the observed misallocation of inputs across firms, which is understood to have important implications for productivity growth (Restuccia and Rogerson 2008).

The unexpected hiring mix response of firms to the policy change also suggests that a weakening of employment protection laws could have other collateral impacts which may not necessarily be desirable. These impacts may depend on context-specific factors such as how markets have adapted to the employment protection laws, on interactions with other regulations and the broader institutional environment. In the case of India, this adaptation has taken the form of a dual institution of contractual hiring. More research on how the impact of labor laws depend on such contextual factors will be useful.

Our results also underline the need for more research on regulatory enforcement. They suggest that there is something in the way IDA is enforced that caused a change in a specific provision (Chapter V-B, in our case) to have broader impacts. More research on the long term impacts of Rajasthan’s labor law deregulation, such as its impacts on firms long-term investments in technology, would also be interesting. This could be explored in the future using more years of post-treatment data.

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