Misallocation and Capital Market Integration: Evidence From India

A measurement problem and a policy problem. On measurement, “it is common to attribute all – or much of – the cross-sectional dispersion in the observed marginal returns to firms’ inputs to misallocation. This creates upward bias in measures of misallocation and can contaminate estimates of differences in allocative efficiency across countries or over time” (§1, p. 2), with the paper’s own footnote listing the sources: measurement error, model misspecification, productivity volatility combined with costly input adjustment, unobserved technology heterogeneity, and informational frictions. On policy, even a perfectly measured aggregate cost of misallocation “is mostly silent on what policies would be required to reduce misallocation in low-income countries,” because the indirect approach does not identify which characteristics causally drive residual dispersion (§1, fn. 2). The paper is also careful about scope from the outset: “reducing misallocation” here means among formal-sector firms within treated manufacturing industries, and “we cannot speak to the global effects of the policy on misallocation, as this would require us to be able to observe the universe of firms and FDI worldwide” (§1, fn. 3).

Because foreign capital could either relieve or worsen domestic credit frictions, and both stories have support. “On the one hand, in low-income countries, where formal credit markets are limited, opening up to foreign capital markets might reduce funding constraints if foreign investors have better screening technologies or are not bound by domestic historical, political, or regulatory constraints. On the other hand, foreign investors may be worse at processing and monitoring soft information, particularly in low-income countries, thereby worsening the allocation of capital” (§1, p. 3), with the paper citing evidence that foreign banks in low-income countries lend mainly to large domestic firms. The paper also notes its result runs opposite to Gopinath, Kalemli-Özcan, Karabarbounis and Villegas-Sanchez (2017), who find that a capital inflow raised misallocation in Spain, and gives two reconciling reasons: equity and debt may work differently – “Equity encourages investors to invest in firms with high upside potential, while debt may encourage investment in ‘safe’ firms with high levels of collateral” – and baseline financial development differs sharply between India and an OECD country (§1, pp. 7-8).

Through a first-order expression for the change in the treated industries’ Solow residual, in which the input-reallocation term is the sales share times the output elasticity times a function of the ex-ante wedge times the change in the input. Following Petrin and Levinsohn (2012) and Baqaee and Farhi (2019), the paper derives an approximation whose second term makes the prediction operational: “the Solow residual (and therefore output) will increase if the amount of x used by firms with relatively higher wedges for x… increases” (§2, pp. 9-10). Two implications matter. First, misallocation can fall even while total capital in the treated industries rises: “Increases in total capital will reduce misallocation as long as ex-ante high wedge firms grow faster than low wedge firms” – expansion of high-wedge firms need not come at low-wedge firms’ expense. Second, the expression is deliberately assumption-light: it “does not require any assumptions about returns to scale, cross-good aggregation, the joint lognormality of TFPR and TFP, or the shape of input-output networks,” in contrast to the standard result under which the variance of log TFPR is a sufficient statistic only if TFPR and TFPQ are jointly lognormal, production is constant returns, and output is a CES aggregate.

Industry-level grants of automatic approval for foreign direct investment and/or increases in the foreign-equity cap to at least 51 percent, with the study confined to post-2000 episodes to avoid the early-1990s reform wave. Before 1991 the Foreign Exchange Regulation Act (1973) required every instance of foreign investment to be individually approved and capped foreign ownership below 40 percent in most industries; the 1991 reform made investment up to 51 percent automatically approved in certain industries, and thereafter different industries liberalised at different times (§3.1, pp. 11-12). The paper collected the timing from editions of the Handbook of Industrial Policy and Statistics and matched it to 5-digit NIC industries. Restricting to 1995 onward means “we only exploit policy variation from the 10% of manufacturing firms who experienced foreign capital liberalizations in the 2000s,” where 45 percent of manufacturing firms are in industries liberalised at some point (§3.3, p. 15). After dropping a handful of 1998 liberalisations (104 firm-year observations, 0.26 percent of the sample) to preserve a longer pre-period, “the only remaining liberalization episodes occurred in 2001 and 2006.”

The timing is documented; the industry selection is not, and the paper treats that as a threat to be tested rather than assumed away. India’s contemporaneous Economic Surveys describe the 2001 reform as a “remedial measure” for “widespread industrial slowdown” and the 2006 reform as part of a “comprehensive review of FDI policy” undertaken to “consolidate the liberalization already effected and further rationalize the FDI policy” (§3.1, p. 13). By the early 2000s both major parties agreed on promoting FDI, and the binding problem was a decline in inflows, which “pushed the government to promote reforms in industries that had not yet been deregulated.” But the Surveys “offer less insight into why specific industries were chosen,” and the paper flags that Chari and Gupta (2008) found politics did shape the 1991 reform, with more concentrated industries and those with more state-owned firms less likely to liberalise: “If similar political motives also dictated the choice of industries liberalized in 2001 and 2006, this may affect our estimates.”

Prowess, a firm-level panel from the Centre for Monitoring the Indian Economy, covering more than 70 percent of economic activity in India’s organised industrial sector and 75 percent of corporate taxes collected – representative of large and medium-sized firms, not of small or informal ones. The paper defends this on theoretical grounds drawn from its own aggregation equation: changes in the Solow residual are driven by changes in inputs to firms with large sales shares, so “changes in inputs to firms with a very small sales share (e.g., the informal sector) will have little effect on the Solow residual unless they release inputs to larger firms, and if those larger firms are in Prowess, we will still be able to detect these changes” (§3.2, p. 14). Analyses are supplemented with the Annual Survey of Industries for robustness. The rare feature Prowess offers is product-level detail: Indian firms must disclose product-level capacities, production and sales under the 1956 Companies Act, so total product sales and total quantity sold are both reported at the firm-product level across 1,400 distinct products, permitting unit prices and quantities (§3.2, pp. 14-15). Two known limitations: Prowess has no employee counts, so labour is measured by the wage bill; and units are not standardised across or within firms, so 2 percent of product observations are dropped. The final sample is an unbalanced panel of 5,013 firms across 337 5-digit industries and 63,149 observations, after restricting to manufacturing, to 1995-2015, to firms with computable pre-2001 MRPK and MRPL, and after dropping observations with year-on-year revenue declines greater than 85 percent (8 percent of the sample; results are “virtually unchanged” without this restriction).

As revenue divided by capital, which is proportional to MRPK within an industry under a revenue Cobb-Douglas production function with a common capital elasticity. The derivation is explicit (§4.1, p. 18): under the revenue Cobb-Douglas form, MRPK equals the capital elasticity times revenue over capital, so revenue/capital “provides a within-industry measure of MRPK, under the assumption that all firms in an industry share the same” capital elasticity. Capital is total tangible physical assets. To classify firms, MRPK is averaged over 1995-2000 and a firm is “high MRPK” if its average exceeds the 4-digit industry median. Separately, TFPQ is constructed by Levinsohn-Petrin estimation using Wooldridge’s GMM at the 2-digit industry level, then netting out a sales-share-weighted average of the firm’s product prices; the paper flags that the LP identifying assumption “does not require that capital or labor are not misallocated – the key sources of misallocation that we study in this paper – but does assume away misallocation of materials,” and that with only 43,791 firm-year observations available, “we view our within-firm productivity results as more exploratory than our main misallocation results” (§4.1, pp. 18-19).

That absent the reform, high-MRPK firms would not have grown relatively faster than low-MRPK firms in treated versus untreated industries – which the paper calls “fundamentally untestable” and then supports three ways. Firm fixed effects absorb any time-invariant difference between treated and untreated industries and between high- and low-MRPK firms, so “our specification does not require that the reform was randomly allocated, nor does it require that firms must have the same pre-treatment characteristics” (§4.3, pp. 20-21). The three supports are: event-study figures showing parallel pre-trends both between treated and untreated industries and in the high-minus-low-MRPK difference; insensitivity of the coefficients to high-dimensional fixed effects, including 2-digit industry-by-year, 5-digit industry-by-year (which absorbs the main reform effect entirely, leaving only within-industry-year variation) and state-by-year; and a battery of industry-level regressions showing that nothing predicts which industries were reformed. That last table is worth stating precisely: the ex-ante log variance of MRPK, the number of firms, average firm capital, export share, the state-owned sales share, the Herfindahl index, and the level and growth of industry FDI all fail to predict liberalisation (§4.3, Table 2, pp. 21-22). The paper offers reasons the 1991-era political correlates might not recur: the 2001 and 2006 reforms were smaller, the context had flipped from external pressure to courting FDI, and the 2000s reforms “have been characterized as disorganized.”

Non-random treatment via fixed effects and the predictability test; endogenous foreign flows by never using observed flows as the regressor; and measurement error in MRPK by arguing it attenuates. On endogeneity: “while it is likely that, within an industry, foreign capital is targeted towards specific firms, we do not use observed variation in foreign capital in our regressions. Instead, we exploit an exogenous shifter to the amount of foreign capital an industry can receive” (§4.3, p. 23). On measurement error: firm and year fixed effects absorb error that is firm-specific and time-invariant or time-varying and common; classical error in the outcome does not bias point estimates; and misclassification of the high-MRPK indicator “will lead to attenuation bias… this would lead us to underestimate the change in these firms’ wedges due to the policy” – with the honest caveat that “non-classical measurement error could still bias our results in the other direction.” And an important conceptual point: the test does not require foreign investors to identify high-MRPK firms at all. Investors might fund large, well-established low-MRPK firms already saturated with capital, reducing their demand for domestic bank credit and thereby “freeing up resources that could then be redirected to smaller, high MRPK firms,” making the effect on high-MRPK firms “a ‘by-product’ of greater access to capital at the industry level.”

Yes at the industry level, and suggestively at the firm level, concentrated in ex-ante high-MRPK firms. Aggregating Prowess’s “Equity Composition” module (available from 2001, covering listed firms, under a quarter of the sample) to the industry-year level and normalising to 2001, foreign equity grows faster in industries liberalised in 2001 than in never-liberalised industries, “and the effect is even more striking for industries that liberalized in 2006… as there is a clear trend break after 2006” (§5.1, p. 24). The honest limitation is stated: there is no pre-period for the 2001 cohort. At firm level the paper uses two proxies rather than equity directly: foreign loans reported to the Reserve Bank of India from 2004 under External Commercial Borrowings, and CMIE’s CapEx record of whether a firm’s large capital projects (10 million rupees or more, roughly $135,000) were foreign-owned. Ex-ante high-MRPK firms differentially increase any access to foreign debt by 6 percentage points and their total foreign debt by 96 percent, and are differentially more likely to have a foreign-owned project and to spend more on one (§5.1, Table 3, pp. 25-26). The paper is careful about what this shows: CapEx “certainly undercount[s] foreign capital flows,” the debt result covers only the 2006 reform with two pre-treatment years, and “while certainly not conclusive, these results are consistent with ex-ante high MRPK firms receiving more foreign capital.”

Capital up 32 percent and MRPK down 18.7 percent for the average firm, both significant at 5 percent; revenues and the wage bill positive but insignificant. Dropping the interaction term, the average capital effect corresponds to roughly $3.7 million per firm in the post-treatment period based on 2000 levels, while the wage-bill estimate is “borderline significant with p = .12” (§5.2, Table 4, pp. 26-27). The reason the average is insufficient is the paper’s central logic: “when firms have heterogeneous MRPKs, the positive effect of increasing capital on treated industries’ aggregate output can be amplified or attenuated depending on which types of firms (those with high or low MRPK) benefit more.”

Relative to low-MRPK firms, high-MRPK firms raise physical capital 53 percent, revenues 23 percent and wage bills 28 percent, and cut MRPK 33 percent – and low-MRPK firms move essentially not at all. In dollar terms the paper puts these at roughly $5.6 million of capital, $8.5 million of revenue and $0.9 million of wages (§5.3, Table 5, pp. 29-30). Three features carry weight. First, the labour result is not a substitution story: “Higher investment does not crowd-out labor… suggesting that there may be important complementarities between capital and labor.” Second, the MRPK gap narrows but does not close: since high-MRPK firms’ MRPK was more than twice that of low-MRPK firms before the reform – the paper elsewhere puts the average gap at 160 percent – “the reform shrank but did not fully eliminate the gap.” Third, the asymmetry is itself informative for measurement: because wedges fall for high-MRPK firms with no effect on low-MRPK firms, “even if the assumption of lognormality of TFPR held before the policy change, it would be violated afterwards,” so the standard variance-of-log-TFPR statistic would not be valid here.

The paper addresses both directly. On mean reversion, the first line of defence is the absence of a symmetric effect – low-MRPK firms do not revert upward. Beyond that, the results survive assigning high-MRPK status using shorter pre-treatment windows (1995-1997, 1995-1998) and using only the 2006 reform, in each case leaving a gap between the classification window and the reform (§5.3, p. 29). On the staggered-treatment bias highlighted by Goodman-Bacon (2021) and de Chaisemartin and D’Haultfoeuille (2022), the paper argues the bias should be small because “the vast majority of our observations are not treated during the study period (around 90%),” and then shows results are quantitatively similar when each treated cohort is compared only to the never-treated group.

Slowly: the headline magnitudes take three to four years to materialise, the full effects at least five years, and at ten years the capital and MRPK effects are +79 percent and -46 percent. The event studies show no differential effect on high-MRPK firms before the policy and a progressive build afterwards, which the paper attributes to slow-moving input adjustment – worker flows, adaptation of production tools – and possibly to competitive effects that also operate gradually (§5.3, pp. 31-33). Separate event studies for high- and low-MRPK firms confirm the asymmetry: “the reform has no effect on low MRPK firms across outcomes, while high MRPK firms’ outcomes change sharply following the reform.” A composition result accompanies this: high-MRPK firms raised the share of capital held in plants and equipment by 4 percentage points, with no effect for low-MRPK firms.

They are largest where the pre-reform state banking sector was least developed, which the paper reads as evidence that domestic banking inefficiency is part of the source of misallocation. Local financial development is proxied by the log average bank credit of all scheduled commercial banks in a state over the pre-reform years 1995-2000, entered as a triple interaction (§3.4 and §5.3, Table 8, pp. 39-40). Two supporting observations: the pattern is hard to reconcile with a differential-trends explanation, since “for differential trends to explain these results, they would have to vary systematically with states’ financial development”; and pre-reform MRPK dispersion is itself higher in less financially developed states. The paper’s reading is that “under-developed domestic banking markets are an important source of misallocation in India… and that foreign capital liberalization can act as an alternative for developing the banking sector,” and it quotes Anne Krueger, then IMF deputy managing director, writing that Indian banks “are considered to be very high cost and inefficiently run.”

Prices fall 17 percent on average and 21 percent in total for high-MRPK firms; product-level output rises 27 percent on average with the increase concentrated in high-MRPK firms; and high-MRPK firms add products while low-MRPK firms add fewer. The product regressions add firm-by-product fixed effects, so they are identified off changes in price or output for a given product made by a given firm and “are not biased by the addition or the deletion of products” (§5.4, Table 9, pp. 41-42). The differential price effect for high-MRPK firms is significant only at the 10 percent level (and corresponds to about 12 percent relative to low-MRPK firms), with the 21 percent figure being the total effect for those firms. Output rises 24 percent for high-MRPK firms relative to low-MRPK firms, and “we cannot reject a 0 effect on low MRPK firms’ output.” On portfolios, high-MRPK firms raise the number of products offered by 3 percent and are almost 10 percentage points more likely to offer new products, while low-MRPK firms are 8 percentage points less likely to add new products and no more likely to delete them – a pattern the paper reads as “the initially high MRPK firms expanding into new areas, crowding out expansions by low MRPK firms.” The paper offers two channels for the price decline and does not choose between them: lower marginal costs passed through, and greater product-market competition compressing mark-ups.

Yes: high-MRPL firms raise wage bills 24 percent and cut MRPL 28 percent relative to low-MRPL firms, closing about a fifth of the MRPL gap. The motivation is that labour has a fixed-cost component through wage rigidity and hiring and firing costs, so “when there is a mismatch between the payments to labor and the generation of cash-flows, financial constraints may affect employment and labor (mis)allocation” (§5.5, pp. 43-44). Classifying firms by pre-reform MRPL exactly as for MRPK, the wage-bill effect is about $0.5 million, and since high-MRPL firms’ MRPL was at least twice that of low-MRPL firms – the paper elsewhere puts the gap at 130 percent – the 28 percent decline “closes about 20% of the gap.” Industry-level variance of MRPL falls in both Prowess and the Annual Survey of Industries, “though the estimates in the ASI are imprecise.”

By plugging the reduced-form input responses into the Solow-residual decomposition, with the pre-policy wedges identified two ways – and the conservative way sets the post-policy wedge of every ex-ante-taxed firm to zero. Sales shares of net output come from Prowess sales in 2000 scaled using Annual Survey of Industries information on output re-used as inputs; output elasticities come from the production-function estimation; input changes come from the difference-in-differences with heterogeneous effects, under the standard assumption that untreated industries are unaffected – which, the paper notes, “rules out spillovers from treated to untreated industries due to general equilibrium effects” (§6.1, pp. 45-46). Within-firm productivity is set to zero because no significant effect on TFPQ is found. For the wedges, the conventional approach attributes all pre-treatment cross-sectional deviation of expenditure shares from output elasticities to misallocation, with the rental rate of capital set to 10 percent following Hsieh and Klenow (2009) – a choice the paper flags as pushing the estimate up, since “the capital wedges are decreasing in r.” The conservative approach imposes Assumption 1: the policy weakly shrank wedges toward zero without flipping signs, and inputs weakly rose for ex-ante-taxed firms and weakly fell for ex-ante-subsidised ones. Under it, “for a firm with a positive wedge ex-ante, the minimum possible pre-treatment wedge is given by the scenario where, after the policy change, the wedge is zero,” so all post-policy dispersion in marginal revenue products is charged to mismeasurement. The paper defends Assumption 1 from its own results rather than asserting it: MRPK and MRPL fell for above-median firms and not for below-median ones, the declines are much smaller than the pre-existing gaps (160 percent for MRPK, 130 percent for MRPL) so signs are unlikely to have flipped, and capital rose for high-wedge firms and changed little for low-wedge ones. The reason measurement error inflates the conventional estimate is spelled out: because the aggregate expression involves a maximum, and “since maximum is a convex function, increased variance in estimated [wedges], caused by measurement error, will increase the aggregate effect size” (§6.1, fn. 45).

A lower bound of 3.4 percent, 6.2 percent cumulating the policy’s growing effect over five years, 6.0 percent under a non-linear approximation, and 16.3 percent under the conventional approach (§6.2, Table 11, pp. 49-50). Allowing for materials misallocation as well as capital and labour raises the lower bound slightly, to 3.7 percent (§6.2, fn. 47). The cumulative figure exists because the static difference-in-differences assumes constant treatment effects while the event studies show effects growing, so “using estimates from a standard difference-in-differences that assumes constant treatment effects over time may lead row 1 of Table 11 to underestimate the long-run effects”; re-computing with the five-year estimated effect gives 6.2 percent. The non-linear approximation, built by estimating year-by-year effects and chaining them, comes out at 6.0 percent, “quite close to the simpler, cumulative first order approximation” – which is the paper’s evidence that higher-order effects are not driving the result. The paper also states what this object is not: the expression “cannot be used to calculate the counterfactual effects of alternative policies or to measure the effect of eliminating all misallocation in the Indian economy,” and it differs from the sufficient-statistics approach of Sraer and Thesmar (2020), which scales a policy up to the whole economy, because “the object we bound [is] the aggregate effect of the policy that was actually enacted.”

They are broadly in line with estimates for the 1991 FDI liberalisation, and the paper names employment, distribution and the informal sector as unfinished. Benchmarking is “limited by the sparsity of the literature on misallocation and foreign capital liberalization,” but Bollard, Klenow and Sharma (2013) and Sivadasan (2009) both find large aggregate productivity gains in sectors affected by the 1991 reforms, “on the order of or even larger than the range of potential aggregate effects we report” – with two qualifications: those liberalisations happened during a macroeconomic crisis, and although both papers attribute most gains to within-firm productivity growth rather than reallocation, “their decompositions may systematically underestimate reallocation’s contribution to productivity growth” (§6.2, pp. 50-51). The conclusion is careful about mechanism: “Our pattern of results is consistent with foreign capital flows directly targeting ex-ante high MRPK firms. That said, it’s also possible that the policy reduced misallocation through other mechanisms, such as by increasing aggregate funding in the industry” (§7, p. 51). And it names the limit imposed by its own data: the focus on firm-level data and the formal sector leaves open “the aggregate employment and distributional consequences of these reforms,” since much manufacturing employment is informal.