Capital Account Liberalization: Theory, Evidence, and Speculation

Allocative Efficiency, drawn from the Solow model, against the sceptical view that the model’s preconditions are absent in developing countries (§1). On the first: “[r]esources flow from capital-abundant developed countries, where the return to capital is low, to capital-scarce developing countries where the return to capital is high. The flow of resources into the developing countries reduces their cost of capital, triggering a temporary increase in investment and growth that permanently raises their standard of living,” citing Fischer, Obstfeld, Rogoff and Summers. The alternative “regards Allocative Efficiency as a fanciful attempt to extend the results on the gains to international trade in goods to international trade in assets,” on the ground that “[t]he predictions of Allocative Efficiency hold only where there are no distortions to the economy other than barriers to free capital flows.” Henry takes Rodrik’s “Who Needs Capital Account Convertibility?” as the representative statement: no correlation between openness and investment or growth, so that “the benefits of an open capital account, if indeed they exist, are not readily apparent, but … the costs are manifestly evident in the form of recurrent emerging-markets crises.”

Not the empirical findings, but the inference drawn from them (§1). Henry accepts the tallies: Edison, Klein, Ricci and Sløk surveyed ten studies and found “only three uncover an unambiguously positive effect of liberalization on growth”; Prasad, Rogoff, Wei and Kose extended this to fourteen studies “but still find only three” – concluding that “there is no strong, robust, and uniform support for the theoretical argument that financial globalization per se delivers a higher rate of economic growth.” His claim is narrower and sharper than a disagreement about results: “[i]t is true that most papers find no effect of liberalization on growth. But these papers tell us nothing about the empirical validity of the theory.” And the design is nearly universal in this literature: twelve of fourteen studies in Prasad et al., nine of ten in Edison et al., eleven of twelve in Calderon, Loayza and Schmidt-Hebbel, and twenty-two of twenty-five in Kose et al. run cross-sectional regressions.

A permanent fall in the cost of capital and a permanent level effect on GDP per capita, with only a temporary growth effect – and long-run growth differences across countries in the model come exclusively from TFP, which liberalization does not affect (§2, §4C). The mechanics are spelled out: with liberalization the marginal product of capital must fall from r + delta to r* + delta, the capital-effective-labour ratio must rise, and “because k*s.state > k_s.state, it follows that at some point during the transition, the growth rate of K must exceed n + g,” which via g(Y/L) = alpha*(k-dot/k) + g temporarily raises output-per-worker growth. Since “differences in long-run growth rates across countries are driven exclusively by differences in their growth rates of total factor productivity (TFP)” and “there is no channel in the model through which capital account liberalization affects TFP growth, strictly speaking, there is no theoretical basis for estimating equation (6).” Henry is explicit that this is a logical point, not a statistical one: “testing whether countries with more open capital accounts invest more or grow faster than countries with closed capital accounts is not logically equivalent to testing whether countries that liberalize experience a temporary increase in investment and growth.”

That a cross-sectional regression can return a negative coefficient on openness in a world where liberalization unambiguously raises growth (§4D). Two small countries share TFP levels and growth rates; A is closed and B fully open, with the world rate r* below A’s domestic rate r, so B has the higher capital-effective-labour ratio and the higher level (but not growth rate) of GDP per capita. A then removes all restrictions for the second decade of a twenty-year window while B does nothing. A’s capital stock growth, and therefore its output-per-capita growth, rises temporarily, so “A will have a higher average growth rate for the twenty-year period under consideration than Country B.” But A’s SHARE is 0.5 and B’s is 1.0, so “regressing GROWTH on SHARE would produce a negative coefficient on SHARE, with the attendant (and specious) conclusion that liberalization exerts a negative impact on growth.” Henry’s conclusion is about power as much as bias: “[t]he strictly cross-sectional regression framework is simply powerless to detect the effect.”

It is binary, silent about what was liberalized, and cannot be mapped to any model (§3A, §4A). SHARE is the fraction of years line E2 of the IMF’s AREAER judged a country free of “Restrictions on payments for capital transactions.” Because “[t]he presence of a bullet point in line E2 indicates that the country has some form of restrictions,” the underlying judgement “takes on the value one if any capital controls are in place and zero otherwise.” Worse, “the AREAER provides no information on the specific aspect of the capital account that was liberalized. Because the underlying data provide no indication of what has been liberalized, neither can any index that is based on such data. Without any indication of what drives the variation in SHARE, it is also unclear how to map that variation to a well-articulated model.” The concrete cost: inflow and outflow liberalizations have opposite predictions – easing inflows in a capital-poor country lowers its cost of capital and temporarily raises growth, whereas “if that same developing country were to liberalize capital outflows nothing would happen to its cost of capital, investment, or GDP” – and E2 cannot tell them apart.

Henry treats it as a genuine improvement in measurement but of limited use for the developing-country question, and notes it still tests for permanent effects (§3B). Quinn scores capital account receipts and payments 0 to 2 each in half-point increments, giving a CAPITAL index from 0 to 4, and finds a positive and significant correlation between growth and changes in CAPITAL. Two limitations: the non-OECD data “end in 1988, and therefore do not include the most rapid period of capital account liberalization in the developing world (the late 1980s and early 1990s),” so “Quinn’s results may reflect the impact of the move from closed to open capital markets among the developed nations” – Henry notes that between 1973 and 1988 the number of OECD countries scoring 2 or lower fell from 11 to 1 while the number of developing countries scoring 2 or lower rose from 26 to 32. Second, “Quinn, like Rodrik, also uses a strictly cross-sectional regression framework, so his results imply that easing restrictions on capital account transactions have permanent effects on growth. Since theory predicts only a temporary effect, it is not clear how to interpret this result.”

Henry concludes not, while explicitly declining to dismiss institutions as substantively unimportant (§3B). Klein and Olivei, on 67 countries from 1976 to 1995, find a significant SHARE-growth correlation “but the developed countries in the sample drive the results” with no significant correlation among the non-OECD countries. Edwards, interacting openness with 1980 GDP per capita for 20 countries, finds “an open capital account positively affects growth after a country achieves a certain degree of economic development”; Arteta, Eichengreen and Wyplosz object on three specific grounds (Quinn’s measure used only for 1973 and 1988, weighting observations by 1985 GDP per capita, and questionable instruments) and find “a fragile association.” Kraay likewise finds no conditional relationship. Henry’s verdict is hedged both ways: “while future work may prove otherwise, it seems fair to say that the absence of significant results in the cross-sectional literature is not a consequence of failing to condition their tests on the level of institutional development,” with a footnote reading “[w]hich is not to deny the importance of institutional considerations.”

By the first verifiable occurrence of a decree, a first country fund, or a jump in the investability index – accepted as narrow precisely because narrowness buys a clean prediction and a high signal-to-noise ratio (§5). Since “in many cases there is no obvious government declaration or policy decree to which one can refer,” the literature uses the first closed-end country fund establishment date (“since one presumably needs government permission to establish a fund”) or a large jump in the International Finance Corporation’s investability index, “the ratio of the market capitalization of stocks that foreigners can legally hold to total market capitalization.” Henry defends the narrowness directly: “it is precisely the narrowness of stock market liberalizations that make them more useful than broad indicators … Since measurement error reduces the statistical power of any regression, it is important to focus on policy experiments where the true variation in the data is large relative to noise,” and unlike SHARE “there is no theoretical ambiguity about the expected impact of lifting restrictions on the flow of capital into the stock market of a developing country.” The cost is sample size: “relatively few developing countries have a stock market, publish reliable stock market data, and also implemented a liberalization.”

Yes, conditional on an empirical regularity about emerging-market return variances (§5A). Under uncertainty the investment condition becomes expected marginal product equal to r + gammaVar(r_M) + delta, where gamma is the price of risk. Liberalization changes both terms: the interest rate falls to r, and “the equity premium after liberalization is equal to the price of risk times the covariance of the local market with the rest of the world.” So “liberalization will reduce the cost of capital if the variance of the domestic market return is greater than its covariance with the world market.” That is an assumption with an empirical warrant rather than a theorem: “[h]istorical stock returns show that this condition holds for emerging stock markets (Stulz, 1999b).” Henry also flags what he is holding fixed: “[f]or expositional convenience, I assume that liberalization has no effect on the marginal product of capital.”

Falling cost of capital, rising investment, faster growth – in the directions theory predicts (§5B). On prices: “[i]n a sample of 12 emerging economies that liberalized between 1986 and 1991, the average country experienced a revaluation of 26 percent in real dollar terms,” with liberalizations coinciding with “an average fall in dividend yields of 5 to 75 basis points.” Henry notes the robustness of the sign if not the size: “[w]hile the magnitude of the effect differs slightly depending on the sample of countries and the exact liberalization dates applied, there is broad agreement across all policy-experiment studies that liberalization reduces the cost of capital.” On quantities: for the 18 countries in Table 1 “the raw growth rate of the capital stock rises from an average of 5.4 percent per year in the five years preceding liberalization to an average of 6.5 percent in the five-year post-liberalization period”; “in a sample of 11 emerging economies, stock market liberalization leads to a 22 percentage point increase in the growth rate of real private investment,” with only two of the eleven lacking abnormally high investment in the first year and only one in the second; and “Bekaert, Harvey, and Lundblad (2005) find that the growth rate of GDP per capita increases by a percentage point per annum.”

Because liberalizations arrive inside a package of reforms, and because the decision to liberalize is plausibly endogenous with no credible instrument (§5C, §5D). On the package: Table 1’s columns show that stock market liberalizations coincide with inflation stabilization, trade liberalization and privatization, each independently good for asset prices, investment and growth, and many countries also received Brady Plan debt relief. This matters specifically for the dividend-yield evidence, since in the Gordon model D/P = r - g^e, so “[i]f the growth rate of dividends does not change with liberalization, then a fall in the dividend yield implies a fall in the cost of capital” – but “there is a strong possibility that large changes in expected future growth rates do occur at the same time that countries liberalize.” Controlling for reform dummies leaves the liberalization effects “statistically and economically significant,” yet endogeneity remains: “politicians may be more inclined to open up when times are good,” and “one is struck by the distinct lack of variables that are correlated with the decision to liberalize but uncorrelated with the stock market or macroeconomic fundamentals” – political regime change fails because it brings new economic programs too. Henry’s conclusion is a calibration instruction rather than a dismissal: the correlations “require a measured interpretation.”

Three candidates; the survey rejects the first and leaves the other two open, while naming the measurement gap it would take to settle the question (§6A). The puzzle: liberalization raises market value “by roughly 30 percent in real dollar terms,” large for an event study but small given how much lower developing-country capital-labour ratios appear to be. First candidate, incremental liberalization – countries “seldom move from having a completely closed stock market to one that is fully open” (Korea began with country funds in 1982, started lifting its statutory ceiling only in 1992 and finished in 1998) – is rejected because “stock market responses to liberalizations subsequent to the first are fairly small,” and the continuous investability-index approach gives “a cumulative fall in the dividend yield … about 140 basis points.” Second, returns may simply not be much higher in developing countries because weak institutions depress TFP: on the Hall-Jones social infrastructure measure “the median G-7 country ranks fourteenth of 130 countries, while the median emerging economy ranks sixty-fourth,” with similar patterns on the Heritage, Ease of Doing Business and Global Competitiveness indices. Third, returns are higher but capital market imperfections – agency problems, asymmetric information, weak investor protection – keep the differential from being arbitraged; the 18 liberalizing economies “rank lower than developed countries on every commonly used measure of investor protection.” Henry identifies the binding constraint on resolving this: “there are few studies that attempt to measure the rate of return to capital in developing countries directly. In my view, this continues to be an important gap in the literature,” and the policy-experiment sample of at most 25 countries lacks the power to test the cross-sectional prediction that liberalization should matter more where investor protection is stronger.

No, and the survey works the arithmetic out explicitly before arguing the fund date is a proxy rather than the mechanism (§6B). Chile liberalized in May 1987 via the Toronto Trust Mutual Fund, “a Canadian closed-end fund with a net asset value of 37.7 million US dollars.” With 1987 market capitalisation of 5.34 billion dollars and a market-to-book ratio of 0.7, the book value of listed assets was about 7.63 billion; five years of the observed 2.2 percentage points of abnormal annual capital-stock growth “adds an additional 890 million dollars of productive assets,” so “[t]he 37.7 million dollar capital inflow can account for less than five percent of this increase.” Three facts persuade Henry the dates are still informative: a steady stream of subsequent country funds and ADR issuances (Chile saw “6 additional country funds with a cumulative net asset value of 991.8 million dollars … between 1987 and 1992”), and aggregate net equity inflows rising sharply after the median country-fund date; no reversal of foreign access after any Table 1 date except Malaysia in 1997-98; and a rise in capital-goods imports, with liberalization leading to “a 6-percent increase in capital goods as a fraction of total imports” and a 12 percent rise in the machine-imports-to-GDP share across 25 countries liberalizing between 1980 and 1997.

No – and this is the survey’s most pointed criticism of a finding that superficially supports its own thesis (§6C). “[T]he increase in the capital stock following liberalizations is too small to account for the observed increase in growth. Bekaert, Harvey, and Lundblad (2005) find that the increase in economic growth due to liberalization is about one percent per year after controlling for a number of variables. This estimate is implausibly large.” The arithmetic: capital growth rises about one percentage point and “the elasticity of output with respect to capital is roughly one-third. Therefore, a percentage-point increase in the growth rate of the capital stock cannot raise the growth rate of GDP per capita by much more than one-third of a percentage point.” The residual must be TFP, and measured TFP growth did rise “from an average of 0.19 percent per year in the five years preceding stock market liberalization to an average of 1.82 percent per year in the subsequent five years” – but “one cannot glibly attribute the increase in TFP growth to stock market liberalization,” because the model’s channel runs through capital accumulation only. FDI could bring technology, but “Mexico is the only country in Table 1 whose liberalization date (May 1989) also coincides with a major easing of restrictions on FDI,” and while plant-level productivity gains from foreign ownership are documented in Mexico and Venezuela, “[t]here is no evidence … that plant-level productivity gains generate economy-wide knowledge spillovers that stimulate higher aggregate TFP growth.”

The survey says the inference does not follow, and names the missing evidence (§6C). Both links are documented – “capital account liberalization within a country does tend to increase its financial development,” and “countries at high levels of financial development allocate capital more efficiently than countries at low levels” – but “[t]he temptation, of course, is to invoke transitivity … The problem with such logic is that documenting a positive correlation between the efficiency of capital allocation and financial development in a cross section of countries does not permit us to infer that more financial development within a given country will improve its allocative efficiency. Without a convincing body of time series evidence that the quality of a country’s capital allocation improves as its level of financial development rises, no basis exists for concluding that liberalization indirectly improves the efficiency of domestic capital allocation.” Henry is careful to leave the mechanism live rather than refuted: “I am not arguing that one cannot tell stories in which capital account liberalization increases higher TFP growth” – easing liquidity constraints, or risk sharing encouraging riskier higher-growth technologies – “[t]he point is that … there is simply no intellectually sound way to draw such a conclusion from aggregate data.”

They confirm the asset-pricing side of the risk-sharing story and the investment response on average, and decisively fail to confirm that investment tracks firm-specific risk (§7A-7B). At the firm level the pre-liberalization hurdle rate carries an equity premium proportional to the covariance of the firm’s return with the local market, and afterwards with the world market, so the change in the cost of capital is (r - r*) + gamma*DIFCOV, giving two predictions: a common intercept across firms in a country, and revaluations increasing in DIFCOV. Both hold: “[i]n a sample of 430 firms from 8 countries, the average firm-level revaluation is about 15 percent in real dollar terms, changes in firm-specific covariances explain roughly one-third of the revaluation, and the common shock is the same for all firms,” with corroboration from EU accession, where “the difference between the beta of a firm’s stock return with the local market and its beta with the European market explains about 22 percent of the typical stock price revaluation” in 74 firms. On investment, the common-shock prediction holds and is larger than the aggregate figure – “[t]he growth rate of the average firm’s capital stock exceeds its pre-liberalization mean by an average of 3.8 percentage points per year … much larger than the corresponding increase in the aggregate capital stock over the same time period (1.1 percentage points per year)” – which Henry treats as making the real-effects case more credible, since listed firms are the ones directly affected. But the firm-specific prediction fails outright: “[t]here is no evidence that physical investment responds to changes in systematic risk, and firm-specific changes in equity premia (the DIFCOV variable) have an economically trivial and statistically insignificant effect on changes in investment.” He does not soften it: this “delivers a powerful blow to the Allocative Efficiency view of liberalization,” while noting the counter-argument that testing CAPM-consistent physical investment in developing countries “may seem to fly in the face of all common sense” – answered with “if the risk-sharing-resource-allocation hypothesis is a straw man, then it is a very popular one,” since virtually all work on international risk sharing rests on the same variance-versus-covariance intuition.

That running the policy experiment backwards is informative, but that its central measure is not a clean test of financing constraints (§7C). Forbes uses El Encaje, Chile’s tax on capital inflows from 1991 to 1998: small publicly traded firms normally show higher investment growth than large ones, which held in Chile before 1991 and after 1998, but “[d]uring El Encaje … the investment growth of small firms drops below that of large firms,” with increased investment-cash-flow sensitivity for small listed firms and no change for large ones. Harrison, Love and McMillan find in cross-country firm panel data that capital account restrictions raise investment-cash-flow sensitivity, and that domestically owned firms are more sensitive than foreign-owned ones. Laeven finds “the sensitivity of small firms’ investment to cash flow falls by 80 percent as a result of financial liberalization,” with large firms becoming more sensitive, read as evidence they previously enjoyed preferential credit. Henry then states the inferential problem plainly: “[i]f firms face financing frictions then their investment will be sensitive to cash flow. But the converse of the preceding statement need not be true: Sensitivity of investment to cash flow does not imply that firms face financial constraints.”

The survey’s answer is that the question is ill-posed until debt and equity are separated, and that on the evidence available the trouble comes from short-term dollar bank debt (§8, §8A). Three points precede the substance. Crises “occur not in only in countries that liberalize the capital account, but also in those where capital controls are in place,” and “there is, in fact, some systematic evidence that the occurrence of crises and the imposition of capital controls are positively correlated,” consistent with controls being used “as a way to postpone the financial-market consequences … of weak or deteriorating fundamentals.” Timing is awkward for the causal story: “[t]he median stock market liberalization date in Table 1 is 1989 – five years prior to the Mexican crisis of December 1994 and almost 10 years before the Asian crisis of 1997,” though Henry concedes “the seeds of a misguided policy may take a long time to yield their bitter fruit, so lags in timing alone cannot dismiss the possibility.” The substantive distinction is contractual: “servicing an equity contract involves procyclical payments that tend to stabilize the balance of payments, whereas debt service payments are countercyclical and therefore have the opposite effect,” and short-term interbank loans “adjust through quantities” while portfolio flows adjust through prices. The Asian numbers make the point: at end-1997 “55 percent of foreign bank loans world-wide were short-term, and one third of these loans were of the interbank variety”; the five crisis countries received 47.8 billion dollars of bank loans in 1996 and suffered a 29.9 billion dollar outflow in 1997, “a reversal of almost 80 billion dollars in a one-year period,” whereas portfolio flows “fell by about half but remained positive,” and in Thailand portfolio flows actually “increased by 70 percent between the second and third quarters of 1997.” Henry also notes the general result that “the ratio of short-term debt to reserves predicts crises.”

Partly history, partly political economy the survey explicitly labels speculation, and partly identifiable distortions in the international financial architecture (§8B). From 1970 to 1984 “debt typically accounted for about 80 percent of all capital flows to developing countries,” the immediate reason being that “[p]rior to the latter half of the 1980s, developing countries largely banned foreigners from holding domestic shares.” Stock market liberalization changed the mix substantially – portfolio equity rose from under 0.1 percent of total inflows in 1980-84 to 18.7 percent in 1990-95, debt fell from 82 to 50 percent, FDI rose from 13 to 28 percent – but “developing countries still lean heavily towards debt.” On why governments opened debt inflows before equity markets, Henry flags his own tentativeness: the competing explanations “deserve more serious consideration than the speculative treatment I give them in the next few sentences” – domestic capitalists wanting cheaper capital but not the preconditions, banks losing monopoly rents, large firms fearing competition from newly financed smaller rivals. The architecture argument is more concrete: Basel I required capital of at least 8 percent of risk-adjusted assets but weighted short-term non-OECD loans at 20 percent against 100 percent for long-term ones, so that “short-term, foreign currency lending to banks in emerging markets required only one fifth of the capital required of long-term loans … and no more capital than a long-term loan to a bank in an OECD country.” Henry adds Rogoff’s three further sources of debt bias: deposit insurance and implicit bailout subsidies, the fact that “[t]he international financial system protects the rights of debt holders more vigilantly than those of equity holders” (G-7 courts hear debt disputes but offer no analogous recourse for G-7 holders of emerging-market equity), and the underdevelopment and opacity of emerging equity markets.

That the textbook theory survives once tested on its own terms, and that the attachment to cross-sectional growth regressions is a matter of habit and disciplinary taste rather than evidence (§9). “There is little evidence that economic growth and capital account openness are positively correlated across countries. But there is lots of evidence that opening the capital account leads countries to temporarily invest more and grow faster than they did when their capital accounts were closed.” On why the field kept asking the other question: “[p]art of the answer is tradition. Cross-sectional regressions of national growth rates on policy variables have been around for a while, so the gravitational pull of that methodological approach is quite strong. But I also think that the answer has something to do with a professional obsession. There has always been a great deal of interest in uncovering policies that increase the steady-state rate of growth. As a consequence, economists tend to ignore the importance of short-run increases that permanently raise the path of national income to a higher, but parallel trajectory.” The policy claim in the introduction is correspondingly asymmetric rather than a blanket endorsement: liberalization of debt flows, “particularly short-term, dollar-denominated debt flows – can cause problems,” whereas “all the evidence we have indicates that countries derive substantial benefits from opening their equity markets to foreign investors.”