The Impact of Lifting Firing Restrictions on Firms Evidence from a State-Level Labor Law Amendment

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.


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. 1 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. 2 Some of them may be rolled out country-wide as part of a new federal labor code currently under consideration. 3 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. 4 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. 5 Moreover, since the IDA has not been amended significantly by any state after 1989, most index-based studies essentially rely on crosssectional variation for identification.
The amendments made Rajasthan's labor laws more pro-employer. Most prominently, the em-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). 6 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. 7 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. 8 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. 9 But, there was a significant increase in their employment of contract workers. There is 6 The 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). 7 Having 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. 8 We 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. 9 We use the terms factory, manufacturing establishment and firm interchangeably; the primary unit of analysis is a factory. 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). 10 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 10 Our conceptualization of the implicit labor tax is similar to that in Hsieh and Klenow (2009). of contract hiring. 11 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. 12 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. 13 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. 14 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-11 It 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). 12 For example, Besley and Burgess (2004), Ahsan and Pagés (2009), Hasan R. and Ramaswamy (2007) and Aghion et al. (2008). 13 See, for example, Bentolila and Bertola (1999) and Di Tella and MacCulloch (2005), and the survey in . 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). 14 See, for example, Hsieh and Klenow (2009) and Hsieh and Klenow (2014).
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

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. 15 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. 16 15 Establishments 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). 16 Chapter 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 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. 17 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). 18 A number of regulatory requirements other than the Factories Act also start binding at the threshold employment sizes of 10 or 20 workers. 19 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. 17 Hasan R. and Ramaswamy (2007), Ahsan and Pagés (2009), Gupta, Hasan andKumar (2009) andOECD (2007). 18 Similarly, the regulation of smaller manufacturing units, shops, and other types of small workplaces is laid out in the Shops and Commercial Establishments Acts. 19 They 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.
in that industry. 20 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)).

Rajasthan's labor law amendments
Rajasthan passed several amendments to industrial labor laws in November 2014. 21 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). 20 Section 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. 21 See G.o. Rajasthan (2014c), G.o. Rajasthan (2014a) and G.o. Rajasthan (2014b) 3 Methodology

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 Y st 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, Z s 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 µ s , and e st 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 1t , 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 JX1 vector of weights w * j such that (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 Z s ) 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 w * J ) in a post-intervention period t will be close to the counterfactual Y 1t , pro-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 w * j are selected to minimize the distance between the predictor variable values of the treatment unit (that is, X 1 ) and the synthetic control (that is, the weighted mean X s of the control group). 22 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. 23 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 22 This 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. 23 The 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 w j 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 w * j weights) for the best fitting convex combination of the control units. Among the three approaches for selecting a starting point, the approach that gives the best result is then adopted. 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.

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, y it is an outcome of interest in firm i and year t. P ost t is a dummy for post-treatment years, T reat i is a dummy equal to one if firm i had 100-300 regular workers in the baseline year, and Rajasthan i is a dummy equal to one if the firm i is located in Rajasthan. The regression includes year-specific dummies Y ear t and firm fixed effects µ i . 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 employment above 300) across Rajasthan and other states. The P ost t × T reat i 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 P ost t × Rajasthan i 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.

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 γ t s) on the key interaction term T reat i × Rajasthan i . The omitted year dummy corresponds to the baseline year. Hence, the γ t s measure differences relative to the baseline year. A systematic pattern in the γs 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 γs 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 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) 24 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. 25

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). 26 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 Q it is the level of production that the firm is trying to minimize costs for. P L it and P M it are the price of labor and material, respectively. We assume that these input prices can vary across 24 These states were shortlisted based on average GDP per capita from 2012 to 2015 25 Note 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. 26 The 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). firms, but cannot be affected by the firm (that is, the firm acts as a price taker in factor markets).
τ L it and τ M it are the implicit taxes on labor and materials, respectively. They are not paid explicitly (that is, not included in the firm's reported expenditure on the factor).
It can be shown that the firm's first order condition for labor and material are as follows: Here, ρ it is the firm's output price markup. θ L it and θ M it are the elasticities of output with respect to labor and material, respectively, and depend on the production function. κ L it and κ M it are the 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 τ L it as the relative 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 over time in study period. Then the input elasticity term log( 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.

Data and descriptive statistics
The main data source for this paper is India's Annual Survey of Industries (

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. 27 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.

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.

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. The share of contract labor is about 6-7 percentage points lower in larger control firms, across

Firm-level descriptive statistics
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. 30

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  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. 30 As 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  Table   14 in the appendix shows the match between Rajasthan and the synthetic control in terms of the predictor variables, and the weights assigned to the potential donor states in the synthetic control.
The synthetic control tracks Rajasthan's output closely in the pre-treatment period, but a significant gap in output opens up after 2015. On average, Rajasthan's output is 21 percent higher than the synthetic control's output in the post-treatment period. This suggests that the reform had a positive impact on output. However, the placebo tests are not fully supportive of this inference.
Panel B presents the MSE ratios from the placebo tests. Although Rajasthan has a larger MSE ratio than all the placebos, the gap between Rajasthan's ratio and the largest MSE ratio among the placebo states is not sizable. It implies that the likelihood of obtaining an impact estimate as large as that for Rajasthan when the treatment is assigned at random is 0.16.   is that on RJ * T reatment * P ost. 31 It captures the differential post-2015 change in the outcome of treated firms (those with baseline employment between 100-300) relative to control firms (those with baseline employment above 300) across Rajasthan and other states. Note that these regression control for contemporaneous nation-wide shocks that varied across treatment and control firm size groups through the T reatment * P ost term, and for shocks that varied across Rajasthan and other states but affected firms in both size groups equally through the Rajasthan * P ost term. The standard errors are clustered by firm to account for serial-correlation in firm-level shocks.
The estimated impact on the log of total employment is positive (0.031) but statistically not significant (column 1), suggesting that the amendment had no sizable impact on total employment.
The estimated impact on the log of contract worker employment is 0.81, and it is statistically significant at the 1 percent level (column 2). This indicates that the amendment increased contract worker employment by about 124 percent. In contrast, the estimated impact on the log of permanent worker employment is negative (significant at the 10 percent level) and indicates a 19 percent reduction in the permanent workforce (column 3). 32 Hence, the share of contract workers in total employment is estimated to have increased by 10 percent (column 4). Part of this increase is on the extensive margin, with the share of firms using any contract workers estimated to have increased by 14 percent points (column 5). 31 All lower degree interaction terms are included in the regression, but not shown in the tables for the sake of concision. 32 As shown in the summary statistics in table 12 in the appendix, the average baseline share of contract workers in total employment in the treatment group is 20 percent. Give the values of the estimated impacts in percentage terms, this implies that treated firm experienced a roughly equal increase in contract workers and decrease in permanent workers in absolute terms, leaving total employment unchanged.
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. 33 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.)

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 33 Instead 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.
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. 34 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.
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.) 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.
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.
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.

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. 35 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 35 Firms with fewer than 20 contract workers were already exempt from the CLA The results presented so far do not make any distinction between permanent and contract labor when estimating the implicit labor tax; that is, they consider the total labor expenditure of the firm. Using data on labor expenditure disaggregated by permanent and contract workers, we can also examine if the estimated impact of the IDA amendment on implicit labor costs is driven by contract labor. To do so, we treat permanent and contract labor as separate inputs in a Cobb-Douglas production function and estimate changes in their respective implicit costs. The results, shown in Table 8, suggest that it was the implicit cost of contract labor, and not permanent labor, that fell among treated firms (columns 1 and 2). Splitting treated firms into those with fewer and more than 50 contract workers at baseline, we observe that the decline in the implicit cost of contract labor is larger in firms that had more than 50 contract workers at baseline (columns 3 and 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.
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 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 * T reatment * P ost term in the difference in differences regression. 36 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. 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.)

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.