The real effects of capital controls: Firm-level evidence from a policy experiment

Because Brazil ran the most active and best-documented controls episode of the period, and because the IOF can be changed overnight by decree, which makes the announcements plausible surprises (Section 1, pp. 2-3; Section 2, pp. 5-7). Four advantages are listed: Brazil “applied a series of capital controls measures that ranged across debt, equity and derivative instruments between 2008-2013,” with “detailed information about the policy changes as they relate to specific instruments and magnitudes”; “a precise set of announcement dates that facilitate a clean identification strategy”; stock market and comprehensive firm-level financial statement data; and “access to proprietary export data from the Brazilian export authority (Secex) for the listed Brazilian firms,” which matters because “coverage of foreign sales data is very poor in the widely used Worldscope data.” The surprise element is institutional rather than assumed: “Under the Brazilian Constitution, the National Congress by law has to approve most tax increases and changes usually take effect after ninety days. However, the IOF is an exception – a ‘policy decree’ can modify the tax that ranks below a law and does not require Congressional ratification.” The authors corroborate this with external evidence: “Using data from investor interviews, Forbes, Fratzscher, Kostka, and Straub (2016) document that investors did not anticipate the controls.”

A sequence of IOF impositions, expansions and removals from March 2008 to mid-2013, widening from debt to equity, derivatives and ADRs (Section 2, pp. 4-7). Against a currency that “appreciated by 50% to 1.6 R$/US$” in 2008 from a low of 3.1 in 2004, and inflows the Institute of International Finance put at a rise “from US$11.2bn in 2006 to US$79.5bn in the following year,” the government introduced a 1.5 percent IOF on incoming foreign fixed-income investment in March 2008. It was eliminated in October 2008 as the crisis reversed the flows – “Net foreign capital inflows dropped from US$88.3 billion in 2007 to US$28.3 billion in 2008,” with net foreign portfolio investment in debt and equity falling “from US$48.1 billion in 2007 to -US$0.77 billion in 2008.” Controls returned as early as February 2009, and on 20 October 2009 the IOF was set at 2 percent covering fixed income plus portfolio and equity investments, though “the IOF did not apply to inflows of direct investment.” On 5 October 2010 the fixed-income rate went to 4 percent and “less than two weeks later the tax was raised to 6%.” March 2011 brought 6 percent on foreign loans of up to 360 days’ maturity, extended to two years by early April, alongside eight consecutive Selic cuts “from 12.5% in late August 2011 to 8% in July 2012.” Unwinding began with the removal of the 2 percent equity IOF in December 2011, the removal of the tax on foreign investment in local debt and the 1 percent currency-derivatives tax in the first week of June 2013, and the elimination of reserve requirements on banks’ short dollar positions on 1 July 2013.

Negative abnormal returns from the cost-of-capital channel – but the paper is explicit that the cash-flow channel can point the other way for some firms (Section 3, pp. 24-27). The price-wedge logic from Black (1974) and Stulz (1981) gives the baseline: the two models differ in whether the tax falls on net or on gross long and short holdings of risky foreign assets, but “both models show that the world market portfolio will not be efficient for any investor in either country,” and Stulz “also shows that under some conditions the domestic investor’s portfolio may altogether preclude a subset of foreign securities.” Mapped to an event study, “an increase in expected returns and a fall in stock prices will be reflected in negative cumulative abnormal returns (CARs) in the event windows surrounding capital control announcements.” The offsetting channel is stated before any result is reported: “if the controls alter the expected value or variance of the domestic production activities, the impact on a firm’s stock price will depend on two effects: the expected cash flow effect and the required rate of return or cost of capital effect. A priori, some firms can benefit from the protectionist variety of capital controls. … For example, exporting firms may benefit from protectionist capital controls if the exchange rate depreciates and expected future cash flows go up.” That is why the exporter result later in the paper is ambiguous between two explanations rather than evidence for one.

Two-day cumulative abnormal returns against a market model with Scholes-Williams betas, estimated 280 to 30 days before each event, pooled into a firm-event panel with bootstrapped p-values (Section 3.1 and Section 4, pp. 27-34). The short window is a deliberate identification choice: the authors examine two-, three-, five-, eleven- and twenty-one-day windows but “present results for the two-day windows in our main specifications as this is the most stringent identification test we can apply to capture the announcement effect of the capital controls with less concern about other confounding news events.” Scholes-Williams betas are used because “nonsynchronous trading of securities introduces a potentially serious econometric problem of errors in variables to estimate the market model with daily returns data.” Because some events are close enough together that their estimation windows overlap, the authors also run the analysis “using the estimation window prior to the October 2009 event as the benchmark return in the CAR calculations for all the following events.” The market return is the BOVESPA index, with the IBRA index as an alternative. One event is excluded by construction: the 22 October 2008 removal of the IOF, because it coincided with “a massive decline in the US stock market … the S&P 500 index fell by 6.1% and the Dow Jones Industrial Average recorded a loss of 514 points, or 5.7%,” though the authors report the results are robust to including it.

With bootstrapped p-values in the reported tables and two-way clustering as a check, because the standard event-study independence assumption fails here (Section 5.1.1, p. 33; Section 5.3, pp. 78-80). The problem is spelled out: “When aggregating abnormal returns, typical event studies assume that abnormal returns are not correlated across firms. … The assumption is reasonable only if the event dates for individual firms do not overlap in calendar time. In the case of a capital controls event, however, all Brazilian firms share identical event dates. Given that the capital control announcement dates are clustered in time, cross-sectional correlation of returns may result in biased standard errors and potentially incorrect inferences (Petersen, 2009). Standard event study methodology is therefore not appropriate for capital control announcements.” The response is Petersen’s two-way clustering, “relaxing the assumption that abnormal returns are not correlated across firms and time” and allowing nonzero off-diagonal elements in the variance-covariance matrix; those results are not reported but described as available from the authors, and the main tables report bootstrapped one-tailed p-values following Busse and Green (2002).

CARs fall about 0.28 percent on average, rising to 2.66 percent once size is controlled for – because size captures substantial heterogeneity that pulls the unconditional average toward zero (Section 5.1.1, pp. 34-36). “Quantitatively CARs fall by about -0.28% on average over a two-day window for the full sample of events,” significant at 1 percent. Adding lagged log total assets, “the coefficient on the constant term suggests that the CARs fall on average by a quantitatively significant -2.66% at the 1% level, which is an order of magnitude higher than the simple regression in Column 1 that does not control for firm size. This suggests that firm size captures an important dimension of underlying heterogeneity at the firm level.” The size coefficient itself is positive and significant at 1 percent, so “large firms were somewhat shielded from the imposition of capital controls.” Leverage adds nothing: “Including controls for leverage, such as debt to total assets … and short-term debt to total debt, does not appear to have a significant effect on the abnormal returns.”

A one standard deviation larger firm has a fitted CAR about 80 percent less negative – still negative, but much less so (Section 5.1.1, pp. 36-37). Mean log assets is 16.69 and a one-standard-deviation-larger firm has log assets of 18.33. “The coefficient estimates for the mean sized firm give a fitted two-day CAR of -0.29% (-0.0266 + 0.00142*µ Log Assets),” and for the firm one standard deviation larger the fitted CAR is -0.057%, so “a one standard deviation increase in firm size results in a less negative value for the two-day CAR – the difference is about -80.25%. … While the overall effect is still negative for a one standard deviation increase in firm size, the magnitude of the adverse impact appears reduced.” For scale, “the average daily raw return for the sample period is +0.059%.” The distribution of fitted CARs is reported percentile by percentile, and the sign flips only near the top: values “remain negative till the P75 for firm size and become positive for firms with size in the P90 and above.” The confidence intervals are reported honestly in both directions – at the 75th percentile the interval runs from +0.002% to -0.39%, at the 95th from +0.57% to -0.16%, while “confidence interval ranges for firm sizes below P75 are uniformly negative confirming that the negative burden of capital controls policies appears to disproportionately affect smaller listed firms.”

They are less negatively affected, but the paper cannot separate the two candidate reasons (Section 5.1.1, pp. 38-40). Exporter status is “positive and significant at the 5% level,” and disaggregating by export revenue, “smaller exporters in the <$1 million revenue bin do not experience significant returns” while the $1-$100 million bin is positive and “statistically significant at the 15% level.” Two mechanisms are offered without adjudication. The first is financing: “large firms can rely on internal capital markets or other sources of financing to fund their operations in the aftermath of controls. Similarly, exporting firms, especially the larger firms, may have access to internal capital markets or foreign currency proceeds and therefore, less reliant on foreign capital investments.” The second is competitiveness: “to the extent that the controls can curb the currency appreciation and improve the competitiveness of exporting firms, the expected future cash flows of the exporting firms can improve in the aftermath of the controls.” A footnote supplies a supporting institutional detail – “the IOF tax rate is zero on foreign exchange transactions related to the inflow of revenue derived from the export of goods and services.”

No – explicitly the opposite, and it says so in its own voice (Section 5.1.1, pp. 41-42). It first states the case for the charitable reading: “A stated goal of the controls was to protect the tradable firms from being hurt by an overvalued exchange rate. Therefore some may argue that the net effect of the controls for an exporting firm is a positive CAR, at the expense of a negative CAR for non-exporting firms is a welcome distributional development of the policy (equivalent to ’taxing’ some firms to ‘subsidize’ exporters).” Then it rejects it on the incidence the estimates actually show: “our results suggest that it is the large firms and large, exporting firms that are the less adversely affected by the capital controls policies – in fact, the estimated coefficients suggest that the overall impact on fitted CARs are positive and significant for the largest firms and the largest exporters. In a developing country like Brazil, it is not clear how subsidizing large exporters at the expense of taxing small firms including smaller exporters and in particular small, non-exporters would be viewed as a desirable. We therefore take the view that the net positive effects on large firms and large exporters are an unintended consequence of the capital controls policies.”

Firms that cannot finance investment internally – via the Rajan-Zingales external finance dependence measure, which is negative and significant at 1 percent (Section 5.1.2, pp. 44-49). Dependence is “defined as capital expenditures minus cash flow from operations divided by capital expenditures,” built from Brazilian firm data. The authors give the reason for preferring this test: following Rajan and Zingales (1998), “it focuses on the mechanism by which the cost of finance affects a firm’s growth prospects, thus providing a stronger test of causality, and it can correct for industry effects.” Fitted CARs make the interaction with export status concrete: “in the high external finance (P75) bin, the fitted CAR value for exporters is -0.37% while it is -0.63% for non-exporters over the two-day event window.” For firms above mean dependence, “the median sized non-exporters (P50) are affected more adversely than the larger non-exporters (P75) with fitted CARs of -0.62% and -0.57%, respectively.” The result survives three alternative definitions – a dummy for above-mean dependence, and the Rajan-Zingales high/low classification restricted to manufacturing – and in the manufacturing sample “firms with high external finance dependence are affected more adversely for both exporters and non-exporters at the P50 and P75 size percentiles.” One companion test comes up empty: an equity-dependence measure (common equity as a fraction of total capital expenditures) is inversely correlated with CARs “but not in a statistically significant manner.”

Yes, and equity controls are worse – the equity dummy is negative and significant at 5 percent (Section 5.1.3, pp. 50-55). Fitted CARs separate the two sharply. Under equity-related controls, exporters are negative at every size percentile except the 95th, “ranging from -0.46% for the smallest exporters (P25) to -0.01% for the larger exporters (P90),” while “for non-exporters, the magnitude of negative CARs is much higher ranging from -0.88% for the smallest (P25) to -0.24% for the largest (P95).” Under debt-related controls, “while the smallest exporters are marginally negatively affected, exporters in all other size bins display positive CARs ranging from 0.13% to 0.51%,” and non-exporters below the 90th percentile are negative from -0.41% to -0.25%. Two explanations are given. Surprise: “while Brazil historically experimented with the IOF tax exclusively on debt flows such as in the 1990s, extending the purview to include equity instruments was done for the very first time in October 2009 … The market’s reaction may, therefore, be capturing the element of surprise.” And legitimacy: “controls on debt flows may serve to reduce financial vulnerability given that debt is a non-contingent claim that can generate systemic risk. … Therefore, the market may perceive controls on debt as a desirable means to curb systemic risk or perform a macro-prudential function.” The authors attach two caveats to the debt/equity tests themselves: “given the number of events, the power of these tests is not very high,” and “some events were applied to both debt and equity instruments and, therefore, may be interfering with clean identification when the dummy variables (equity event, debt event) are included in a pooled regression setting.” Estimating debt and equity events separately, which avoids the pooling problem, reproduces the pattern with a statistically different impact across the two groups.

Two pieces: market interest rates rise, and an implied cost of capital computed from analyst forecasts rises – each significant, but at 5 and 10 percent respectively (Section 5.2, pp. 55-63). On market rates, the authors regress changes in the one-, two- and five-year rates over two- and three-day windows relative to the day before each announcement: at the one-year horizon they report “an increase in market rates (3.25 basis points),” while “on average five-year market interest rates rise by 11.8 basis points,” significant at 5 percent. (The tabulated one-year coefficients are not significant at conventional levels, and the five-year two-day coefficient of 7.24 basis points is significant only at the 15 percent level, so the five-year three-day estimate is the one carrying the claim.) The authors explain the term-structure pattern: “The more muted response of the one-year rate may be the result of it being a direct instrument of monetary policy or the policy rate. The term-structure effects are however more direct measures of the market’s response to the unexpected capital controls announcements.” The directional point they emphasize is that this runs against the global backdrop: rates rise “against the backdrop of quantitative easing in the US and other developed countries that put downward pressure on the world interest rate.” The second piece follows Hail and Leuz (2009), using Easton’s (2004) modified price-earnings-growth model solved for each firm’s implied cost of capital from IBES one- and two-year-ahead EPS forecasts and one-year-ahead dividends, in 14-, 21- and 28-day windows before and after each event, with both roots of the quadratic used. A t-test finds the cost of capital “significantly higher at the 10% level in the 14-day window for both the maximum and minimum root values,” and in regressions “the post-event dummy is positive and statistically significant at the 10% level of significance” in the 14- and 21-day windows – but “not statistically significant in the 28-day window (not reported).” The exporter asymmetry recurs: “the effects of announcements are smaller for exporting firms.”

The sign is right and the significance is absent (Section 5.2, pp. 63-66). Using daily Real/dollar data, “the coefficients on the exchange rate variable are negative but not statistically significant. A negative coefficient suggests exchange rate depreciation consistent with the motivation behind capital controls to curb currency appreciation by stemming the inflow of foreign capital. However, the lack of statistical significance precludes us from drawing robust inference from the result.” The narrative record points the same way: the Real “steadily appreciated between January 2007 and July 2008 and, despite a brief period of depreciation during the onset of the Global Financial crisis, continued to appreciate between January 2009 and July 2011,” reaching R$1.6 by early 2011, which Brazil’s finance minister Mantega attributed to US quantitative easing while the IMF’s Western Hemisphere director pointed instead at China’s peg. The authors’ own summation is agnostic about which force dominated: “while the imposition of controls may have been motivated by trying to stem the appreciation of the Real by curbing the inflow of foreign capital from developed countries such as the United States, alternative international economic forces such as the undervalued Remimbi may have rendered such attempts unsuccessful.” A footnote records the closest existing verdict: Chamon and Garcia (2016) find the controls “were effective in partially segmenting the Brazilian financial market from the international markets,” but “do not seem to have deterred the appreciation of the real when capital inflows were strong.”

Robust across return models, event windows, indices, size proxies, subsamples and liquidity controls; and more negative under a fixed estimation window (Section 5.3, pp. 66-78). The regressions are re-run with raw returns, standard CAPM and Scholes-Williams betas, over two- and three-day windows, and for the IBRA as well as the BOVESPA index, “obtaining similar patterns.” Adding event dummies to allow for the varying size of each IOF change – “the October 2010 event increased the IOF tax by 33% more than the March 2008 event” – leaves the overall effect “negative and significant.” Subsamples of multinational subsidiaries, ADR issuers (where the constant is -0.0305, significant at 10 percent, and where “approximately 40%” of Bovespa constituents are secondarily listed in New York, with a 1.5 percent IOF imposed on ADRs converted into local stock in November 2009), and firms that issued bonds abroad all reproduce the pattern. Bank debt share is negative but insignificant; operating revenue as an alternative size proxy is positive and significant at the 15 percent level; and three Datastream turnover-based liquidity measures, included to address the concern that “Brazil’s market, even amongst Bovespa constituents, can be quite illiquid,” leave the results intact. Using the MSCI world index in a world-CAPM framework gives similar patterns. The most informative check runs the other way: re-estimating with a single invariant estimation window prior to the first event, “the CARs are significantly more negative,” because that pre-period was a capital-inflow surge and a booming stock market, so “the abnormal returns in the period following the controls are even more negative and statistically significant at the 1% level.”

No – loosening events produce no detectable market response at all, and the paper offers competing readings without choosing (Section 5.3, pp. 74-77). With a loosening dummy in the pooled specification, the dummy is “negative but not significant” and “the overall effect on the CARs remains negative and significant.” Estimating the two types separately, tightening events reproduce the benchmark – “the CARs fall on average by a quantitatively significant -2.27% at the 1% level” with size controlled – while “for loosening events in contrast, the constant is not significant in any specification. All other variables that condition for firm characteristics such as size and exporter status are also not significant.” Three possibilities are floated: reduced statistical power, since “the number of events and observations is substantially reduced when limiting to loosening events”; selection in the timing of removals, since “the restrictions were removed when there is limited demand for Brazilian assets”; and genuine asymmetry, since “the controls were increasingly tightened before they were gradually removed.” A footnote reports that re-estimating with an invariant pre-first-event estimation window leaves the non-response robust.

The firms most likely to be hurt (Section 5.1.1, pp. 42-43). “Systematic firm-level financial data for small, unlisted firms are not available for these Brazilian firms. Disclosure requirements for listed firms provide access to firm-level financial statements. Further, our empirical methodology relies on estimating cumulative abnormal returns based on stock market data that are also only available for firms that are listed on the stock market. Our results show that from the listed sample, the firms that are most adversely affected are the small, non-exporters. This evidence therefore also suggests that our results may suffer from attenuation bias in that we do not have the smallest, unlisted firms in the sample. In some sense one can argue that our evidence provides a lower bound estimate of the adverse impact of capital controls on the cost of capital for Brazilian firms.” A second boundary is worth noting for readers coming to the paper by its title: the source text establishes effects on stock returns, market interest rates and an implied cost of capital, but reports no regression of realized firm investment or capital expenditure on the control announcements, so “real effects” in the title refers to the cost-of-capital channel and its firm-level incidence rather than to measured investment outcomes.

That the optimal-capital-controls literature works with aggregates and debt, while the incidence it documents is firm-level and falls on equity-sensitive, finance-dependent small firms (Section 1, pp. 3-4; Section 6, pp. 82-84). The authors place themselves against “a growing theoretical macro literature [that] posits the benefits of capital controls albeit focusing exclusively on debt rather than equity to motivate the model frameworks (Bianchi and Mendoza 2010, Farhi and Werning 2014, Korinek 2010),” and note the empirical literature has been sceptical: Klein (2012) “casts doubts about assumptions behind recent calls for a greater use of episodic controls on capital inflows and finds, with a few exceptions, there is little evidence of the efficacy of capital controls,” while Fernandez, Rebucci and Uribe (2013) “do not find evidence of capital controls implemented as macro-prudential tools in the period 2005-2011.” The conclusion states the implication for modelling: “The findings in the paper have implications for macro-finance models that focus exclusively on aggregate variables to examine the optimality of macro-prudential regulation and abstract from heterogeneity at the firm level. In particular, the evidence in this paper suggests that capital controls disproportionately affect small, non-exporting firms, especially those more dependent on external finance.” It also keeps the size and export offsets in proportion: “quantitatively the data show that the decline in average returns swamps the advantages that firm size for the firms below the 75th percentile and export status offer.”

In both direction and purpose (Section 6, pp. 81-82). “Unlike previous capital controls episodes during emerging market financial crises designed to hinder capital flight, Brazil’s capital controls were devised as a macro-prudential measure to stem foreign capital inflows in the aftermath of the Global Financial Crisis. Brazil also implemented the controls to forestall currency appreciation whereas historically emerging market countries implemented capital controls policies to prevent currency depreciation.” Earlier inflow-control episodes – Chile’s unremunerated reserve requirements in the 1990s, Colombia in the 1990s and 2007, Thailand in 2006 – are noted but judged incomparable in scale: “arguably, these historical examples do not compare to the level of active experimentation in the recent Brazilian experience.” Contemporaneous East Asian measures are also distinguished as piecemeal and bond- or bank-focused: a Taiwanese tax on foreign investment in time deposits, Korean restrictions on FX derivatives trading and foreign-currency lending, an Indonesian one-month time limit on domestic bond investing, Thailand’s removal of an exemption from a 15 percent tax on foreign investors’ domestic bond income.