The Effects of Financial Liberalization on Country-Level Emissions

The paper sets a stewardship channel against a composition channel, and the two predict opposite signs, so the sign is an empirical question. On one side, Dyck et al. (2019) find that institutional investors — particularly from countries with strong beliefs about environmental and social issues — cause companies to improve their environmental and social performance, and Döring et al. (2023) find that firms with foreign institutional investors are more likely to report greenhouse gas emissions, with reporting firms more likely to reduce them (Powers et al. 2011, Tomar 2023). Since liberalization brings in foreign institutional investors, this predicts lower emissions. On the other side, Hart and Zingales (2017) argue that public firms underweight social surplus relative to private firms and so produce more negative externalities, and Shive and Forster (2020) find empirically that otherwise similar private firms pollute less than public ones. Since liberalization is followed by growth in the size of existing public firms (Kim and Singal 2000, Henry 2000a, 2000b) and in the number of IPOs — Huang (2014) documents Taiwanese IPOs rising more than 100% after liberalization — this predicts higher emissions. The paper states them as H1a (a reduction) and H1b (an increase).

Because firm-level effects need not aggregate: firms can move polluting activity rather than reduce it, and only a country-level measure captures entry, exit and reallocation together. The authors point to evidence that local pressure can push firms to relocate polluting activities — to other plants within the same company, to subsidiaries, or by selling assets to companies less sensitive to environmental concerns (Aragon-Correa, Marcus, and Vogel 2020, Bartram, Hou, and Kim 2022, Bisetti et al. 2022, Duchin, Gao, and Xu 2024). A country-level aggregate nets these out. The authors are explicit about the cost: “the number of country observations is much smaller than what can be examined at the firm level; thus, there is a loss of precision with country-level studies”, and they present the two levels as complementary rather than one superseding the other.

By a simple indicator that switches on in the year a country officially liberalized, for the 41 countries dated by Bekaert, Harvey, and Lundblad (2005). The episodes run from Japan in 1983 through the 1990s, and most occurred in the late 1980s and early 1990s. The authors note that Bekaert, Harvey, and Lundblad also provide measures of liberalization intensity, but follow the common practice — they cite Moshirian et al. (2021) — of using a binary indicator instead. Liberalization has a sample mean of 0.20 across the 7,680 country-year observations, so a fifth of the panel is in the post-liberalization state.

EDGAR, the Emissions Database for Global Atmospheric Research, for three pollutants; and absolute emissions with GDP as a control, rather than emissions divided by GDP. Version 7.0 supplies fossil-fuel carbon dioxide and aggregate greenhouse gases in CO2 equivalents for 1970–2021; version 6.1 supplies sulfur dioxide for 1970–2018. The authors give two reasons for preferring totals. Conceptually, absolute emissions correspond to how policy frameworks are written — national carbon budgets and international mitigation targets are defined in total quantities. Empirically, following Bolton and Kacperczyk (2023), intensity ratios “can make large emitters appear to improve simply because output expands”, and dividing by a volatile denominator such as GDP adds noise unrelated to emissions performance. The dependent variables are the logarithm of emissions plus a constant chosen to set skewness to zero, and the authors report that not deskewing has no significant impact on the results. They also report that normalizing pollution by GDP instead of controlling for it produces similar results.

A staggered two-way fixed-effects difference-in-differences design following Callaway and Sant’Anna (2021), with country and year fixed effects and standard errors clustered at the country level. Results are reported twice, once using only never-treated countries as controls and once also admitting not-yet-treated countries. All specifications control for log GDP, log population, temperature deviation from the country’s 1960–2019 average, and indicators for corporate governance reforms (coded by Fauver et al. 2017) and mandatory environmental disclosure (from Krueger et al. 2024, updated using Carrots & Sticks and ESG Book). GDP and population come from CEPII’s CHELEM database and temperature deviations from World Bank data; additional specifications add imports and exports, control of corruption, and regulatory quality from the World Bank Worldwide Governance Indicators. Note that the text describes GDP as the log of annual domestic product while Appendix A defines the variable as the log of GDP per capita, so a reader should check which is intended before interpreting the population coefficient.

Liberalization is followed by economically large increases in all three pollutants, with the 10-year effects roughly double the 5-year ones. Using not-yet-treated countries as controls — the more conservative column — the log-point estimates are 0.129 and 0.197 for carbon dioxide over the [+1, +5] and [+1, +10] windows, 0.084 and 0.139 for greenhouse gases, and 0.080 and 0.155 for sulfur dioxide, corresponding to the 13.8%/21.7%, 8.8%/15.0% and 8.3%/16.8% increases quoted in the paper’s introduction. With never-treated controls the estimates are marginally larger (0.133 and 0.200 for carbon dioxide). All four carbon dioxide estimates in Table 3, Panel A are significant at the 1% level; for greenhouse gases three of the four are significant at 1% and the not-yet-treated 10-year estimate at 5%; for sulfur dioxide the 5-year estimates are significant at 5% and the 10-year estimates at 1%. The authors also note that reading the event-study figure rather than the averaged post-period coefficient, “the final impact on CO2 emissions over the 10-year period is over 30%.”

Yes — the synthetic and stacked estimators give positive and significant estimates for all three pollutants, though not all at the same level. The synthetic difference-in-differences estimator of Arkhangelsky et al. (2021), which chooses weighted controls to match pre-trends, yields 0.135 for carbon dioxide and 0.187 for sulfur dioxide (both at 5%) and 0.115 for greenhouse gases (at 1%), with 1,000 bootstrap replications. A stacked event-study estimator (Cunningham 2021), which builds a cohort of all available controls for each treatment, yields 0.172 and 0.146 for carbon dioxide and greenhouse gases (both at 1%) and 0.125 for sulfur dioxide, the last significant only at the 10% level. The authors also report, without tabulating, that the Mundlak difference-in-differences estimator proposed by Wooldridge (2025) gives similar results.

It shows no significant effect on residential and other small-source emissions, which the authors read as locating the increase in corporate rather than household behavior. The logic follows from the mechanism: if liberalization raises emissions by expanding the publicly traded share of the economy, household emissions should not respond. The estimated effects on the residential-and-other sector are 0.040 and 0.099 for carbon dioxide and 0.025 and 0.082 for sulfur dioxide over the two windows, none significant. The authors are careful about what the category contains: besides residential households it includes “commercial and institutional buildings, agriculture, forestry, fishing, stationary, and farm vehicles”, and they acknowledge that these other sources “could still be impacted”, so the test is a null on a mixed category rather than on households alone. In untabulated tests on the utility and manufacturing sectors they find large increases in both, with carbon dioxide in the utility sector rising over 45% over 10 years, though they note data limitations restrict that analysis.

The authors report little evidence of pre-treatment effects but do not claim none. Their description of the event-study figures is that they “show a marked increase in CO2 emissions after financial market liberalization with little evidence of pre-treatment effects”, immediately qualified: “That said, some pre-treatment periods are significantly positive, although economically the pre-treatment effects are small.” The synthetic difference-in-differences results are relevant here, since that estimator explicitly chooses weighted controls to match pre-trends and returns similar estimates. A second comparability concern — that treated and control countries may simply be different kinds of country — is addressed by dropping all countries whose average GDP, or average GDP per capita, is less than 10% below the poorest of the liberalizing countries; the authors report similar results on that smaller, more comparable subsample.

They are reported for the continuous controls, not for the treatment effect, which the authors flag as potentially inconsistent. Panel B of Tables 3 to 5 reports country-fixed-effects OLS, and the authors state that these specifications “are potentially inconsistent for the primary treatment variable (de Chaisemartin and D’Haultfoeuille 2020), but they allow for additional discussion of the continuous control variables.” In those regressions GDP and population are significantly positively related to carbon dioxide emissions, temperature deviations and corporate governance reforms are negatively related, and mandatory environmental disclosure is not significantly related. Adding imports and exports, control of corruption, or regulatory quality does not change these relations. For sulfur dioxide, better regulatory quality is associated with significantly lower emissions; for greenhouse gases, exports are positively related and corporate governance reforms are not consistently related.

The authors address this three ways, and the placebo result is the one they lean on. GDP is controlled for in every specification; since emissions and GDP are very highly correlated in the sample (0.952 for log carbon dioxide), they also repeat the analysis including a squared GDP term, which is itself significant while leaving the other results maintained; and they note that normalizing emissions by GDP rather than controlling for it gives similar results. Their preferred argument is the placebo: they write that the absence of a household response “is consistent with financial market liberalization affecting emissions through changes in the mix of public and private firms rather than through overall economic growth.” This is an interpretive inference from a null result rather than a direct test of the composition channel — the paper does not measure the public-firm share of the economy directly.

They contrast with two prominent findings and extend a literature that has looked at political rather than financial institutions. Ioannou and Serafeim (2012) find financial institutions largely unrelated to firms’ environmental performance once other national institutions are controlled for; De Haas and Popov (2019) find carbon dioxide emissions lower in countries with more equity-based financial systems. The authors distinguish their approach by focusing on discrete liberalization events and assessing their causal effect on national emissions. The prior country-level work they position against — Congleton (1992) on pollution control and political institutions, Bernauer and Koubi (2009) on democratic institutions and environmental performance, Eskander and Fankhauser (2020) on national climate legislation — is about political or regulatory institutions rather than financial ones. On the growth side they cite Lan et al. (2016) on affluence and population driving energy footprints and Liu, Guo, and Xiao (2019) on economic growth as the dominant force behind greenhouse gas emissions.

They conclude the public-firm expansion channel outweighed the foreign-investor stewardship channel during these episodes, and they are explicit that the period matters. Their statement is that “any reduction in emissions due to foreign institutional investors is significantly smaller than the increase in emissions, as a greater portion of the economy is made up of public firms”, and that the findings “do not support the notion that foreign institutional investors significantly reduce emissions.” They offer a scope condition themselves: the liberalizations studied occurred in the 1980s and 1990s, when global warming was a less salient issue for institutional investors. They then push back on their own caveat — sulfur dioxide was a significant matter of concern in the late twentieth century, and the arrival of foreign institutional investors did not curb those emissions either. For today, they draw the conditional implication that investor stewardship “must be strong enough to counterbalance the structural effects associated with financial market liberalization” and “may need to operate alongside, rather than in place of, environmental regulation.”

The sample is small in the dimension that matters, the mechanism is inferred rather than measured, and the treatment is a single indicator for a heterogeneous set of reforms. Identification comes from 41 liberalization episodes concentrated in the late 1980s and early 1990s, and the authors themselves note the loss of precision inherent in country-level work. The composition channel is never measured directly: no variable in the analysis tracks the public-firm share of the economy, so the mechanism rests on the placebo null plus the prior firm-level literature. The liberalization indicator discards the intensity information available in the source, so the estimate is an average across reforms of differing scope. Some pre-treatment coefficients are significantly positive. And the documentation of the GDP control is inconsistent between the text and Appendix A. The authors’ own framing throughout is that liberalization “is related to” and “is associated with” higher emissions, with the causal language reserved for the difference-in-differences design rather than asserted of the correlations.