Climate policy portfolios that accelerate emission reductions

Domain: neuroscience
Published: 2026-01-23
Editorial outcome: major_revision

Abstract
The corpus of national climate policies continues to grow-but to what effect? Using data on 3,917 policy instruments across 43 OECD countries and major emerging economies from 2000-2022, we show that national climate policy portfolios specializing in instrument types and sectors are associated with faster reductions in fossil CO2 emission intensity. Supported by exemplar country case studies, we also provide quantitative evidence that the effectiveness of climate policy is amplified by long-term emission reduction targets and the presence of dedicated governmental bodies including ministries and intergovernmental organisations. The cumulative effect of all climate policy portfolios over our study period amounts to 3.1 GtCO2 fewer emissions in 2022 relative to a no-policy counterfactual-substantially less than what’s needed to stay on track for the Paris Agreement goals.

Introduction
We are midway through the critical decade for climate change to keep Paris Agreement targets within reach. Global emissions need to peak and decline rapidly by 2030 to ensure near-term progress towards 1.5-2°C climate stabilisation1. Encouraging trends have been observed internationally in 23 countries with declining absolute emissions over more than a decade, and in a further 67 countries with declining emission intensities per unit of economic output2,3. The two major emitters, the USA and China, fall into the first and second groups respectively.

National climate policies help to explain these trends4,5. There are now thousands of climate-related laws and policies in almost two hundred countries6,7. Evidence synthesised in the IPCC’s Sixth Assessment Report attributed 1.3–5.9 GtCO2e/yr of avoided emissions to climate policies including national commitments made under the Kyoto Protocol8–10. Attribution studies use econometric methods to identify the general effect of climate policies on emissions, controlling for other determinants of emission trends. These studies have demonstrated the effect of larger policy stocks11,12, of more stringent policies13, and of specific policy combinations14. The difference-in-differences modelling used by ref. 14 allowed stronger causal attribution but was focused on a set of 69 discontinuities in emission trends from recent policy introductions rather than the cumulative effect of policy portfolios over the long-term.

Policy portfolios have many different elements comprising, inter alia, instruments of different types, coverage of different emitting sectors, and different types of long-term objective setting strategic direction15,16. Policy portfolios are in turn shaped, implemented and monitored by different types of governmental organisation17. The design of each country’s portfolio of climate policies varies in size, specialisation, and organisational context. We contribute an attribution analysis of these different elements of climate policy portfolios across a large sample of countries.

To do this, we analyse the instruments used and sectors targeted by 3917 policies introduced since 2000 in OECD and BRIICS economies [Fig. 1]. These 43 countries account for four fifths of global fossil CO2 emissions18. We extend our dataset to include variables on the presence of different types of long-term national emission-reduction targets and governmental organisations relevant to climate policy effectiveness.

Results
Density & stringency of policy portfolios
We first apply Eskander and Fankhauser19’s model of climate policy density to our more extensive dataset of 3917 policies over the period 2000-2022 (compared with their 1092 policies over the period 2000–2016; see Methods).

The policy density model performs as expected, with faster reductions in CO2 emission intensity observed in countries with larger stocks of climate policies [model 1, Table 1]. This effect controls for the characteristic U-shaped relationship between development stage and emissions, as well as emissions leakage through trade (see Methods and SI1 for extensive discussion on controls and model specification).

To help interpret the policy density model, we replace policy density with policy stringency (which is highly correlated) and show similar results.

Emissions fall faster as climate policy portfolios expand and become more stringent. Policy vignettes for the USA and China illustrate this general insight. The USA has continuously accumulated climate policies since 2000 anchored by milestone federal legislation in 2005 and 2009 on both clean energy production and the efficient use of energy, and more recently in 2021-22 for investment in infrastructure [Fig. 3a]25. These reinforced a secular transition in the energy supply from coal to gas driven by cost and market dynamics.

China was later to start accumulating policies but caught up rapidly from 2005 including through five-year plans beginning in 2006 and 2011 that included energy efficiency and emission reduction targets respectively [Fig. 3b]. By 2022, China had adopted over 245 policies in total, second only to the USA. However, due to its different industrial development stage, China’s emissions in absolute terms are still rising despite its high policy density26.

Brazil provides a counter example of a country with comparatively few climate policies and slow reductions in emission intensity, exacerbated by a weak emphasis on energy and transport sector emissions in its flagship 2009 climate legislation [Fig. 3c]27.

Beyond these simple associations with policy density and stringency, other determinants of emission intensity trends are discussed in the policy vignettes in SI2. These include changing political regimes and priorities towards domestic resource exploitation including shale gas in the USA and oil in Brazil.

Types of instrument in policy portfolios
Countries’ climate policy portfolios vary not just in size and stringency but also in composition. We augment our policy density model [model 1, Table 1] to explore the additional effect of different design features of climate policy portfolios. We start with types of policy instrument.

A common taxonomy of policy instruments distinguishes three main categories: regulatory (rule-based), economic (market-based), and voluntary (participation-based)28.

Using a diversity measure of instrument types, we find countries with higher specialisation on instrument types in their policy portfolios are associated with faster reductions in fossil CO2 emission intensity. This holds for the simple three-category taxonomy (Table S15 in SI1) and for a more granular taxonomy of six instrument types [model 2, Table 1].

In sensitivity testing we find economic instruments have stronger effects than regulatory or voluntary instruments in line with expectations (see Methods and SI1). This is a general finding at the level of policy portfolios, complemented by other studies that pinpoint the effect of specific policy combinations14,24. Specialisation on instrument type is country-specific according to policy traditions (see SI1). Three policy vignettes illustrate the range. Estonia specialises in economic instruments (>50% of all instruments since 2000) including carbon taxes (one of the first in the world), renewable energy feed-in tariffs, electric vehicle subsidies, and energy efficiency incentives [Fig. 3f]30. In contrast, Israel specialises in regulatory instruments (>50% of all instruments since 2012) including rules on renewable energy grid connections and standards for energy efficiency in buildings [Fig. 3d]. Both countries show relatively large reductions in emission intensity.

Indonesia provides a counter example with no specialisation on instrument type and only small reductions in emission intensity [Fig. 3g]. Indonesia’s policy portfolio contains a more diverse selection of instruments, including feed-in-tariffs for renewable energy and standards to enhance energy efficiency in buildings and transport31.

Sectoral coverage of policy portfolios
Climate policy portfolios target GHG emitting groups in different sectors. In most countries the highest emitting sector is either transport or the energy supply. Some countries focus policies on these or other sectors; other countries target economy-wide emissions across all sectors.

Using a diversity measure to characterise the sectoral coverage of national policy portfolios, we find that countries that concentrate on specific sectors reduce their emission intensity faster than those with broader coverage [models 3a & 3b, Table 1] (see Tables S14 and S15 in SI1). As expected, this concentration effect is stronger if coverage is weighted towards sectors with higher shares of national emissions.

Our policy vignettes for China [Fig. 3b] and Israel [Fig. 3d] show portfolio concentration on the energy supply (accounting for 46% and 61% of their respective national emissions from 2000–2022) to boost renewables deployment and accelerate the secular substitution of coal by gas in driving emission intensity reductions32–34.

Our finding on concentrated sectoral coverage is sensitive to the 2020 Covid disruption to sectoral emission trends, particularly in transport, but is robust in the period up to 2019 [model 3c, Table 1], and in the full period to 2022 using an alternative diversity measure less distorted by the 2020 anomaly (see Methods and SI1).

Long-term emission-reduction targets in policy portfolios
Emission-reduction targets are policy objectives designed to steer the general direction of policy portfolios including their constituent instruments. Targets set expectations but vary in form, stringency, and credibility.

We find evidence that both absolute and relative targets amplify the effect of the total stock of climate policies on reducing emission intensity [models 4a & 4b, Table 2] (see Table S3 in SI1). However, faster reductions are observed in countries with absolute targets, which predominantly have Kyoto-aligned 1990 reference years (see Methods). These results hold whether the target is measured in the year it was announced or the later year it entered into legal force. There is insufficient variability in our sample over the period 2000-2022 to isolate the effect of net-zero targets (12.5% of observations).

Policy vignettes for the USA and Mexico illustrate these findings. In 2009, the USA moved from relative to absolute targets, subsequently reinforced by further absolute targets for specific sectors [Fig. 3a]35. This change was consistent with a steady accumulation in the number of policies over the period to 2022 concurrent with falling emissions25. Mexico was an early adopter of framework legislation in 2012 but adopted relative targets that only weakly signalled climate policy ambition36. This coincided with relatively slow progress on emission reductions [Fig. 3h].

Governmental organisations alongside policy portfolios
Climate policy-relevant governmental organisations include: energy or climate ministries with capacity to develop and implement policy; advisory bodies for ensuring accountability and stability over political cycles; and intergovernmental or other international organisations for promoting and diffusing policy ideas and evaluation insights.

We find that countries with dedicated energy and/or climate ministries, and countries that are members of the International Energy Agency (IEA), have policy portfolios associated with faster reductions in emission intensity [models 5a & 5b, Table 2] (see Table S4 in SI1). We find similar effects for membership of the Clean Energy Ministerial (CEM) and the EU-EFTA.

We also test for the effect of independent advisory bodies. However, as these are a relatively recent organisational innovation (11.1% of observations), there is insufficient variability in our sample to isolate their effect on emissions.

Methods
Overall approach
Our econometric approach uses panel regression models with country and year fixed effects for 43 OECD+BRIICS countries over the period 2000–2022. Our dependent variable is fossil CO2 emission intensity per unit of GDP (CO2/GDP), using IEA emissions data. Our main independent variables are policy density, instrument type diversity, and sectoral coverage diversity, using coded IEA policy characteristics data. Using dummies, we also include as independent variables whether countries have long-term emission reduction targets, dedicated ministries, advisory bodies, and are members of intergovernmental organisations. We follow Eskander and Fankhauser19 by including controls in our models for other economic, institutional, and geographic influences on emission intensity including economic development stage, climate zone, and overall governance quality.

To aid the interpretation of the econometric models, we supplement our analysis with climate policy vignettes for select countries that span the range of values on both dependent and independent variables. The policy vignettes describe key milestones and salient issues in the development of each country’s climate policy portfolio over the period 2000-2022. The vignettes are provided in full in Supplementary Information 2 (SI2), and summarised graphically in the main text [Fig. 3].

Data
Descriptive statistics for all our model variables are summarised in Table 3 for 37 OECD and 6 BRIICS (Brazil, Russia, India, Indonesia, China, South Africa) countries over the period 2000-2022.

Dependent variable. Our dependent variable is fossil CO2 emission intensity per unit of GDP using data from the International Energy Agency (IEA)’s CO2 Emissions From Fuel Combustion database. This covers CO2 emissions by sector and by fuel at a highly disaggregated level for almost all countries from 1990.

On average across our 43 country sample, transport accounts for 29% of total CO2 emissions over 2000–2022 and energy supply accounts for 30%. Emission shares from end-use sectors (transport, buildings, industry) vary by economic structure, building stock and heating fuels, transport infrastructure and modal splits. Emission shares from supply sectors (energy supply, energy own industry) vary by domestic resource base, energy industry materialisation, and electricity generation mix.

Independent variables: climate policy portfolios. Our main independent variable is policy density, the cumulative number of climate policies adopted in each country over the period 2000–2022. We also perform robustness checks with pre-2000 policy counts as initial conditions, but these do not affect our results (Table S12 in SI1). We test policy stringency as an alternative independent variable that is highly correlated with policy density and find similar results.

Our additional independent variables are diversity measures of both instrument type and sectoral coverage in national climate policy portfolios, and dummy variables for long-term emission-reduction targets.

To construct our climate policy variables we use the IEA’s Policies and Measures Database (PMD) from which we identified a total of 3917 policies relevant for fossil CO2 emissions for OECD and BRIICS countries over the period 2000–202259. Advantages of the IEA PMD Database over the Climate Change Laws of the World database6 used by Eskander and Fankhauser19 are discussed in SI1.

We then coded all identified policies by instrument type and sectoral coverage. To code IEA PMD policies by instrument type, we use a standard taxonomy distinguishing legal, monitoring, regulatory, market-based, direct provision (e.g. infrastructure investment), information, planning, and voluntary28. There were fewer than 10 occurrences of the legal and monitoring instrument types in our dataset, so for our most granular analysis we combine these with regulatory instrument types to give six instrument types overall.

For more parsimonious analysis we aggregated the instrument types into three commonly used policy instrument categories60:

a. Regulatory (incorporating legal, monitoring, and regulatory policy instrument types)
b. Economic (incorporating market-based and direct provision policy instrument types)
c. Voluntary (incorporating information, planning, and other voluntary policy instrument types)

To code IEA PMD policies by sectors covered, we use the standard energy-related set of two energy-supply sectors (energy industry own-use, and electricity and heat conversion) and three energy end-use sectors (buildings, transport, industry) used for GHG emission inventory reporting to the UNFCCC and in IEA energy statistics. We classified economy-wide or multi-sector policies as covering all five sectors. Policies not matched to any sector are classified as economy-wide policies only and comprise 2% of total observations.

Using our coded IEA PMD policy dataset, we calculated density and diversity measures. First, we construct our basic annual policy density variable to capture the number of climate policies adopted in a country in any given year. As past policies should continue to have an effect on emissions in years following their implementation, we use annual policy density to generate cumulative total policy density such that all past (t-1, t-2,…) and current (t) climate policies are counted at year t within each country. This allows us to measure the cumulative effect of past and existing climate policies on fossil CO2 emissions over the long term. We do not capture policy dismantling (not reported in the PMD). However this is both small and inversely correlated with new policy adoption so its effect is captured indirectly in our models (see SI1)7.

Second, we construct diversity measures for both instrument type and sectoral coverage. To do so, we use the Herfindahl-Hirschman Index (HHI) which is widely used in economics to measure market concentration, and is commonly used in competition and regulatory economics to flag up market power and potential for anti-competitive behaviour61. The HHI takes values between 0 and 1, with 1 representing monopoly. In our case, a higher value of the HHI indicates lower diversity, i.e., higher concentration.

We construct the HHI for each country i by taking for each year t the sum of squares of the share of policy instrument types s2 jt within total policy density (Eq. 1). By using total policy density, we control for the cumulative (long-term) effect of specialisation on changes in fossil CO2 emission intensity.

HHI it= (cid:1)Xs2 jt (1)

For instrument types, we construct HHIs for both for the full taxonomy of six instrument types, and for the more aggregated three category taxonomy.

For sectoral coverage, we construct an unweighted HHI and a weighted HHI that weight policies per sector by that sector’s share of total emissions. This allows us to test whether specialising in policies covering emission-intensive sectors has a larger effect.

As a robustness check in both cases, we also use the Shannon Index as an alternative diversity measure which is less sensitive to anomalous one-off variation that affects sectoral emissions shares in the 2020 Covid year (see SI1).

For long-term emission-reduction targets, we use data from UNFCCC and Climate Action Tracker to construct dummy variables for the presence of absolute targets (% reductions relative to 1990 or other reference year emissions), relative targets (% reductions relative to business-as-usual projections or % reduction in emission intensity or emission intensity per capita), and net-zero targets. For each type of target we code alternative dummies for the year the target was announced and the later year it was ratified. Both dummies produce similar results; we use ratification year in our models.

For absolute targets, we find the 1990 baseline (in line with the Kyoto Protocol) captures most of the variation for target dummies so we use this in our models. Non-1990 absolute targets and net-zero targets contribute only 8.3% and 12.5% of observations.

Independent variables: (inter)governmental organisations. We use data from various sources (see SI1) to construct dummy variables for the presence of a dedicated energy and/or climate ministry, and an independent advisory body (like the UK’s Committee on Climate Change). We also construct dummy variables for membership of intergovernmental organisations associated all or in part with clean energy or climate policy: the International Energy Agency (IEA), the Clean Energy Ministerial (CEM), and the EU (including Switzerland, and EFTA countries: Norway, Iceland, Lichtenstein). As we only consider national policies in our study, the EU dummy captures the interdependence between EU member states (and EFTA trading partners) with regard to their climate policies transposed from EU legislation into national contexts.

Control variables. We use the same set of control variables as Eskander and Fankhauser19 and Nachtigall, et al.13 to account for the political, economic, and geographic determinants of CO2 emission intensity. We distinguish confounders that directly influence emission intensity from secondary controls whose effect is more diffuse. We discuss and substantiate our controls and analyse their impact on our identification strategy in SI1.

We control for three confounders related to economic development stage and structure. We use World Bank data on the log of GDP per capita and its squared term to control for the effect of a country’s development stage and the non-linear (inverted U-shaped) relationship between GDP per capita and emission intensity. We include the share of total economic activity in the services sector to control for the structural shift away from more emission-intensive manufacturing and industrial activities. Additionally, we control for a country’s import dependence by including the share of imports compared to the overall level of economic activity. We expect that a higher import share would indicate more services-oriented countries that import emission-intensive products from other countries with more industrial sector activity (known as ‘carbon leakage’).

We also include three secondary control variables for institutional quality, business cycles, and geography. For institutional quality, we use the rule of law index, estimated by the World Bank on an annual basis for all countries globally, and interpreted as a proxy for policy implementation and enforcement capacity. We expect countries with a stronger rule of law to be more effective in the adoption of climate policies. As our country sample covers only OECD and BRIICS economies, we also expect rule of law to be less decisive as a control variable than in Eskander and Fankhauser19 which included a long tail of less developed economies with weaker and more heterogeneous policy implementation capacity. We include the Hodrick-Prescott GDP filter to control for cyclical volatility in economic activity. Although there is some empirical evidence suggesting that emissions tend to be more cyclically volatile than economic output62, we do not form any strong expectation for this control. We incorporate the annual temperature variation from the long-term average to control for the effect of climatic conditions on emission intensity. We expect an increase in temperature above the long-term average to be associated with lower emission intensities, particularly for countries in the Northern hemisphere with winter heating seasons.

In SI1 we show our controls capture meaningful direct and indirect influences on policy density and are distinct from the country- and time-fixed effects in our models.

Regression models: climate policy portfolios
Our method has three main steps to test observed relationships between the different elements of climate policy portfolios and emission intensity, beginning first with an application of Eskander and Fankhauser19’s model for policy density, before moving sequentially through layers of additional testing and complexity with the policy portfolio variables unique to this study.

Policy density model. Our policy density model follows the specification of Eskander and Fankhauser19 with one main difference: we do not incorporate a short-term policy density variable as a proxy for unobserved (omitted) past climate policies. Our use of the more comprehensive IEA PMD policy dataset includes both past and existing climate polices in contrast to the CCLW dataset used by Eskander and Fankhauser19 which focuses primarily on legislation over other policy types. We therefore have a larger policy dataset (n=3917 IEA PMD policies vs n=1092 CCLW legislations) over a slightly longer time period (2000-2022 vs 1996–2016) but for a smaller country sample (43 OECD+BRIICS countries vs 133 countries).

Our policy density model is shown in Eq. (2):

ln(CO2/GDP)it =α+β 1 Pdens it+β 2 X it+θ ι+η τ+ε it (2)

where ln(CO2/GDP)it stands for the natural log of emission intensity per country i and year t; α is the constant parameter; Pdens it is the total policy density measuring the cumulative number of climate policies per country i for year t; X it is a vector of control variables; θ ι are the country fixed effects; η τ are year fixed effects; and residuals ε it. The use of the natural log in the dependent variable improves model fit and facilitates the interpretation of coefficients such that a one unit increase in policy density would lead to (exp(β)-1)*100% change in the dependent variable.

This model is easy to augment with additional variables for other elements of national climate policy portfolios including specialisation on instrument type and sectoral coverage (see below).

We check the robustness of our models specification by observing whether the coefficients of independent variables and controls change in sign, magnitude, or significance compared with the OECD-only model from Eskander and Fankhauser19. (Coefficients in the two models are not directly comparable due to differences in policy density specification, country and time samples). We expect policy density to be negative and significant as an indication of climate policy effectiveness for reducing emission intensities after controlling for the level of economic activity in each country. This is indeed the case. Our policy density model results are summarised in Table 4 and shown in full in Table S11 and Table S21 in SI1.

In our model the coefficients for GDP per capita and its interaction with the square term, imports share of GDP, and services share of GDP are all statistically significant and with signs in line with expectations (see SI1 for detailed discussion of confounders and controls in our model specification). The OECD-only model of Eskander and Fankhauser19 does not find the GDP terms to be significant which we interpret as being due to lower GDP per capita variation in their OECD-only sample. Other minor differences between the models are shown in Table 4.

As noted our policy density variable is a cumulative measure of all past and existing policies. As a robustness check, we test an alternative model (Table SE, column 2) with a 3-year lagged version of the policy density variable. The model is very similar but the coefficient of the lagged policy density variable is slightly larger in absolute terms. This supports our interpretation that accumulating policy stocks antecede emission intensity reductions rather than vice versa (see below on endogeneity).

Coefficients for the controls are also very similar between these alternative model specifications. Minor exceptions in the lagged policy density model are that the coefficient for Hodrick-Prescott GDP filter becomes weakly statistically significant, and the coefficient for temperature variation increases in magnitude and also becomes statistically significant.

We also directly replicate the model of Eskander and Fankhauser19 with both short-term and long-term policy density variables but applied to our smaller country sample, later time period, and larger policy sample. Again, our results were very similar, with full results shown in Table S11 in SI1.

Interpreting the coefficient for policy density – a count variable - is enabled by the log transformed dependent variable. A one unit increase in policy density is associated with a change in emission intensity of magnitude given by 100% * the exponential of the policy density coefficient minus one. In our base model shown in Table 4, this gives a -0.055% change in emission intensity per unit increase in policy density.

Standardising coefficients using the within-group standard deviation can improve interpretability, particularly when comparing effect sizes across variables measured on different scales. We implement the standardisation procedure proposed by ref. 63. We residualise each predictor with respect to country and year fixed effects, calculate the within-unit standard deviation of the residuals, and use these to standardise the independent variables before re-estimating the model. A one standard deviation increase in policy density (equivalent to ~20 policies) is associated with a -1.1% change in emission intensity. This is comparable in magnitude to the standardised effects of the key confounders (GDP per capita, services share, imports share), and substantially larger than that of secondary controls (rule of law, Hodrick-Prescott filter, temperature variation). See S1 for full results and discussion.

Policy stringency as alternative to policy density. Policy stringency and policy density are strongly correlated. This was demonstrated by Schaffrin, et al.22 with their measure of policy strictness for three countries’ climate policies, and confirmed for a large country sample by the OECD using their own stringency measure, the CAPMF (e.g., Fig 3.2 in ref. 64). Stringency is defined as “the degree to which climate actions and policies incentivise or enable GHG emissions mitigation at home or abroad”.13

The OECD’s Climate Actions and Policies Measurement Framework (CAPMF)64 provides one index on the stringency of climate policies, with sectoral sub-indices (including for buildings, industry, transport, and electricity supply). The index measures the degree to which sectoral climate actions and policies incentivise or enable GHG emissions mitigation. As a country example for the UK, Fig 3.5 in ref. 64 shows that stringency increased with the adoption of more policies over time.

The CAPMF provides a generalisable measure of policy stringency characterising national climate policy portfolios. However, we cannot include CAMPF as an additional portfolio characteristic due to collinearity: it has a 71% correlation with policy density. There are also two mismatch problems. Although the timeframe of the CAPMF is 1990-2022, covering our model period, its OECD country sample does not include Brazil and the United States. The policies covered by CAPMF also do not include many of those coded as voluntary or informational in our policies dataset from IEA PMD.

Consequently, we use CAPMF as an alternative independent variable to policy density for robustness testing our main model, despite the mismatch of policy and country samples. We take the mean of these sectoral policy stringency indices from CAPMF weighted by each sector’s share of total emissions. This is similar to our procedure for constructing emission-weighted diversity indices in our testing of policy sectoral coverage.

We show the full results in Table S20 in SI1. Like policy density, the coefficient for the weighted sectoral policy stringency index is negative and statistically significant at p<.01. A more stringent climate policy corpus is associated with faster reductions in emission intensity. This complements our main finding on the effect of climate policy density.

Policy portfolios specialisation models. Having established our base policy density model, we then augmented it with additional independent variables that measure different elements of climate policy portfolios. First, we control for the effect of specialisation in sectoral policy coverage and instrument type on emission intensities. We incorporate in our base model the HHI measures of diversity. This augmented model is shown in Eq. (3):

ln(CO2/GDP)it =α+β 1 Pdens it+β 2 HHI it+β 3 X it+θ ι+η τ+ε it (3)

where ln(CO2/GDP)it is the natural log of emission intensity per country i and year t; α is the constant parameter; Pdens it is the total policy density measuring the cumulative the number of climate policies per country i for year t; HHI it stands for the Herfindahl-Hirschman Index per country i for year t; X it stands for all controls; θ ι are the country fixed effects; η τ are year fixed effects; and residuals ε it.

We estimate four separate models, one for each of the four HHI variables (see Table 3). Full results are provided in Table S15 in SI1 with model summaries in the main text. We also run robustness checks using the alternative Shannon Index as a diversity measure and find similar results (Table S14 in SI1).

Models 2a and 2b in Table 1 (main text) include the HHIs for six instrument types and three instrument categories respectively. Coefficients for these HHI variables are negative, statistically significant, and are of comparable size. A higher specialisation on instrument type (higher HHI) is associated with larger reductions in emission intensity.

The effect of both policy density and the controls remains virtually identical in both models, and is similar to the base model.

Models 3a and 3b in Table 1 (main text) include the HHI for sectoral policy coverage weighted by the sectoral share of emissions, and the non-weighted HHI. Model 3c in Table 1 shows the weighted HHI for the period 2000-2019 prior to the Covid disruption. After controlling for the 2020 anomaly in sectoral emission shares (see SI1 for details), HHI coefficients are significant and negative. A higher sectoral concentration of policies is associated with larger reductions in emission intensity. The coefficient for the weighted sectoral HHI is almost twice that for the unweighted sectoral HHI. Policy concentration on emission-intensive sectors is more effective. The coefficient for the policy density variable reduces more alongside the unweighted sectoral HHI than for the weighted sectoral HHI, but the augmented model is broadly consistent with the base model. The controls also have very similar effects across the different models specifications.

Policy density model interaction effects with long-term targets and organisations. We use dummy variables to test the interaction between policy density and (1) long-term emission-reduction targets, (2) dedicated energy and/or climate ministries, (3) independent advisory bodies, (4) membership of intergovernmental organisations including the International Energy Agency (IEA) and the Clean Energy Ministerial (CEM).

Following Wooldridge65, we use the model shown in Eq. (4):

ln(CO2/GDP)it =α+β 1 Pdens it+β 2 X it+δ 0 dummy it+δ 1 Pdens*dummy it +θ ι+η τ+ε it (4)

where ln(CO2/GDP)it stands for the natural log of emission intensity per country i and year t; α is the constant parameter; Pdens it is the total policy density measuring the cumulative number of climate policies per country i for year t; X it stands for all controls; dummy it accounts for the presence/absence of targets or organisations; Pdens*dummy it is the interaction term between policy density and the dummy; θ ι are the country fixed effects; η τ are year fixed effects; and residuals ε it.

Interpreting the coefficients in these dummy interaction models is somewhat complex, but in summary the overall estimated effect of total policy density on emission intensity when dummy=1 is given by summing coefficients β 1 and δ 1 (on the condition that both coefficients are significant). If the coefficient for policy density is not significant, we treat it as 0, so we effectively sum 0 to the coefficient for the interaction term. In such cases, the fact that policy density becomes non-significant does not imply that the target or organisation does not help reduce emission intensity. This is because the policy density variable is highly correlated with the interaction term and so they compete for the same effect. (See SI1 for full discussion of the interaction terms and their interpretation).

Models 4a and 4b in Table 2 (main text) summarise the results for absolute and relative emission-reduction targets respectively. Full results are provided in Table S3 in SI1.

For absolute targets (with 1990 reference year), the coefficient for the interaction term is negative, statistically significant, and has about three times larger an effect than the coefficient for policy density in the base model. The coefficient for policy density becomes statistically non-significant, as variation has been picked up by the interaction term, i.e. the countries with absolute targets (62% of the sample).

As a robustness check, we tested an additional model (Table S3 in SI1, column 3) that includes the dummy for absolute targets but not the interaction term. Coefficients for both policy density and dummy are negative and statistically significant. The policy density coefficient becomes non-significant when we include the interaction term.

For relative targets, the coefficient for the interaction term is statistically significant and smaller in magnitude than in the model for absolute targets, indicating relative targets have less of an effect on emission-intensity reductions. In addition, the positive and statistically significant dummy coefficient indicates that these countries with relative targets (5% of the sample) start off with higher emission intensities than the rest.

Both these results hold whether the targets are measured in the year they were announced or the later year when they entered into legal force through ratification.

For the governmental organisations with the exception of dedicated energy and/or climate ministries (50.6% of observations) and membership of intergovernmental organisations (e.g., CEM 29.6% of observations), there was insufficient variation to isolate their effect on emission intensities. Net-zero targets are observed in only 12.5% of observations and independent bodies in 11.1%.

Models 5a and 5b in Table 2 (main text) summarise the results for dedicated energy and/or climate ministries and membership of the IEA respectively. Full results are provided in Table S4 in SI1.

For dedicated ministries, the coefficient for the interaction term is positive, statistically significant, and the sum of the two coefficients is negative but smaller in size than the policy density coefficient which is negative and significant. For membership of the IEA, the coefficient for the interaction term is statistically significant, negative, and larger in magnitude than the coefficient for policy density in the base model, indicating that membership of this international body is associated with a strengthened effect of policy accumulation on emission intensity. Similar results are found for membership of the CEM and EU-EFTA (Table S4 in SI1).

Policy density model: robustness checks & alternative model specifications
We run numerous robustness checks on our policy density model including:

– inclusion of pre-2000 climate policies as initial conditions (Table S12 in SI1)
– exclusion of China (due to large differences in policy counts between IEA PMD and CCLW databases) (Table S12 in SI1)
– 1-year lag on all independent and control variables (Table S13 in SI1)
– replacement of emission intensity with absolute emissions as dependent variable (Table 16 in SI1)

We also test alternative models specifications with subsets of our policy portfolio variables including:

– replacement of HHI diversity measures with Shannon Index diversity measures (Table S14 in SI1)
– policy density for each instrument type (Table S17 in SI1)
– emission intensity for each sector (Table S18 in SI1)

Finally, we test different combinations of control and independent variable including:

– parsimonious controls (Tables S5 and S6 in SI1)
– full combinations of independent variables (Table S19 in SI1)

Results are discussed in SI1. We found no material changes in model results or coefficients in all our robustness tests, and conclude our policy density model is robust to methodological variation and alternative specification. In SI1 we also include full discussion and analysis of confounders and our use of controls.

Endogeneity and reverse causality
In main text we report associations between climate policy portfolios and emission-intensity reductions. Our two-way fixed effects models are not able to establish causality but we interpret our results as showing climate policies are antecedent to emission reductions. As noted, Stechemesser, et al.14 use difference-in-difference (DiD) methods to show that climate policies lead to discontinuous reductions in sectoral emissions within two years of introduction. This shows causality from policies to emission reductions. Our aim is different in assessing the path-dependent effect of climate policy stocks on cumulatively incremental emission reductions (with our additional testing of the interacting role of long-term targets and governmental organisations). We align with the methodological framework established by Eskander and Fankhauser19 in the climate attribution literature and replicate their model specifications for comparison.

In SI1 we address endogeneity issues and provide multiple lines of reasoning to counter reverse causal interpretations of our model results. These include the Durbin-Wu-Hausman test (for endogeneity) and the Dumitrescu-Hurlin test (for Granger causality). We also include arguments and evidence from lagged models, fixed effects, weak correlations between emission intensity with covariates, recent literature, our policy vignettes, and our choice of econometric model. In combination these support our attribution of emission intensity reductions to national climate policy portfolios, controlling for the effect of other influences on emissions.

CO2 emissions avoided due to climate policy portfolios
We calculate avoided CO2 emissions due to climate policy by estimating a counterfactual with no climate policies, following the methodological framework proposed in ref. 19. We set policy density equal to zero in Eq. (2) for our base policy density model, and then subtract it from the full estimated Eq. (2):

ln(CO2/GDP)it - ln(CO2/GDP)it =β^ 1 Pdens it (5)

where we use CgO2it for the counterfactual emissions and CdO2it for the estimated emissions.

However:

ln(CdO2it/GDPit) - ln(CgO2it/GDPit) = ln(CdO2it/CgO2it) (6)

Therefore, combining Eqs. (5) and (6), we get:

CgO2it=CdO2itexp(-β^ 1 Pdens it) (7)

in which estimated emissions can be replaced by observed emissions.

Finally, we aggregate emissions estimated over countries i and time t to calculate total counterfactual emissions under no climate policies as shown in Eq. (8).

CgO2total= X i X t CgO2it (8)

Figure 4 shows the results for the full 43 country sample (left panel) and for the BRIICS country bloc (right panel).

Reporting summary
Further information on research design is available in the Nature Portfolio Reporting Summary linked to this article.

Data availability
In Methods we summarise our variables and the data used in their construction. In Supplementary Information 1 (SI1), we provide further detail on variable construction and data sources.

The data for our independent variables have been stored in the heiDATA repository under the accession code https://doi.org/10.11588/DATA/XTDNAU. The data used to construct our control variables are publicly available and can be accessed via the World Bank (see Table S1 in SI1 for details). The data for our dependent variables on fossil CO2 emission intensity are available under restricted access through the IEA’s Greenhouse Gas Emissions from Energy database (upgrade of the former IEA CO2 Emissions from Fuel Combustion database); access can be obtained through the IEA.

Code availability
The Stata .do file used in our analysis has been storied in the heiDATA repository under the accession code https://doi.org/10.11588/DATA/XTDNAU for replication purposes.

Peer review rounds
[{"round": 1, "reviewer_comments": {"reviewer_1": "The study and its methodology are transparent and well written. I also like the presentation of national figures in the paper and the thorough analysis of national projections in the supplementary information. The study finds quantitative evidence that national climate policy portfolios that specialise in certain instrument types and sectors are associated with faster reductions in fossil CO2 emission intensity. The link with policy instruments is particularly interesting.\nThis study builds on the methodology of Eskander and Fankhauser (2020), but the authors have extended it to a longer time horizon (2000-2019) and cover more policies. The in-depth country analysis of this study is also an added value compared to the 2020 study.\nI think the work could be important in this area, although a better presentation in a chart of the main instrument types and sectors associated with faster reductions in fossil CO2 emission intensity for a selected group of countries would be welcome. As it is, the main policies are included in the figures, but this is widely known.\nThe disadvantage of the method is that it still uses the period that is not very recent, as it misses the last five years where even more policies have been developed, as we also see in the figure, as it misses Fit-for-55 for the EU and IRA for the US. I can understand why you did not focus on the period until 2022 because of the impact of COVID, but the current emissions trend for some countries with many climate policies are lower compared to 2019 levels (Canada, US, EU).\nThere is also an interesting paper in Science on climate policies that have achieved large emission reductions: Global evidence from two decades, which looks at 1500 climate policies implemented between 1998 and 2022 in 41 countries across six continents. It would be good if the authors would also compare some of their results with this study, although I can understand that this study was published after your submission.\nI would recommend publication if the authors adequately address the main comments listed below:\nThe main difficulty I have is with the intensity of climate policy: It is obviously difficult to measure the stringency and GHG reduction impact of all types of climate policies. Nevertheless, the lack of a measure of policy stringency is a major limitation of this paper, because the number of policies is not a good measure of the quality and GHG impact of climate policies. Countries may have many policies and a high policy density, but this does not guarantee that they will reduce CO2 emissions. For example, a single strong national policy based on an ETS with nationwide coverage of all GHGs could be much more effective than multiple policies that have not reduced emissions at all in the end. It all depends on the quality and stringency of the policies and their coverage across sectors to determine the GHG impact. I therefore suggest that the issue of stringency and the GHG impact of policies should be addressed in some way. I assume that the earlier work by Eskander and Fankhauser also addressed this issue.\nI also don't quite understand why the authors use policy intensity in terms of numbers, as this does not take into account total GHG emissions, nor sectoral coverage, and compare it to a country's emissions intensity (i.e. nationwide emissions). I would expect policy density to also be relative to the size of a country's emissions, as well as sectoral coverage. Perhaps you could elaborate on this.\nI think the two tables are not always very attractive to the Nature Communications audience, especially those with many blank cells. A better presentation of Table 2 would be welcome. It would also be good if the authors could present the most effective policies according to their analysis for the major emitting countries.\nPlease use the Nature communications citation and references format.\nSpecific comments:\nYou mention twice: \"National climate policy portfolios that specialise in certain types of instruments and sectors are associated with faster reductions ...\". It would be good to give an example of what you mean by certain?", "reviewer_2": "I would like to thank the authors for a very interesting and timely study on a very important topic. The question of the impact of individual policies and policies cumulatively is highly relevant and hence deserves academic attention. I have a number of concerns that I would ask the authors to address.\nMajor comments:\n1. My main concern about this study is the lack of discussion surrounding causal inference and endogeneity. The paper does not feature a discussion of the basis for the causal inference used in the paper. Are the authors claiming that the policy density is plausibly exogenous? Does the paper claim causality (and how would one avoid claims of reverse causality with higher emissions increasing pressures on governments and then leading to more policies)? Or is this a descriptive assessment? This is especially relevant for wording such as “attributing” different effects as well as for the headline statements that claim that those policies have reduced emissions by such a huge amount. Could those policies be correlated with general economic development or other variables and dynamics? Furthermore, a number of co-variates are likely to be highly correlated (see discussion below with regards to the Energy Ministerial), which is also not discussed. I would expect the authors to discuss questions like these explicitly and to clarify the causality basis that they are making their claims by.\n2. I am highly sceptical about the results concerning the Clean Energy Ministerial as well as the results concerning the presence of an energy ministry. The Clean Energy Ministerial is highly correlated with general institutions in a country (a government/society more focused on climate policy is much more likely to sign up to this). Here, as above, causality is in my mind difficult to claim – as even the direction of causality is unclear. Is the membership leading to more policy diffusion or is policy knowledge in a government leading to joining such an institution? The CEM also (in my experience) plays a negligible role in day-to-day policy-making but is often a publicity exercise. Similarly, the presence of an energy ministry is arbitrary in my view. Every government (that I know of) has a ministry dealing with energy issues, even if it is paired with other dossiers and independent of whether “Energy” appears in the name of a ministry (as I gather from their source Tosun 2018). This is also not a static component – consider for example the German vs the UK case where in Germany the word “Energy” was dropped from the name of the department because climate was added to the ministries responsibility. In the UK Energy remained in the name, but the responsibilities of the ministries changed from BEIS, to DECC, to DENSZ – does Germany deal with Energy less than the UK? I am highly sceptical of those singular dummy variables and would hence suggest to remove them (at the very least from the main text). The same applies to the IEA membership (especially the reverse causality argument) but it is more sensible than the other two.\n3. I notice that the authors have used a dummy for EU membership – but it is unclear to me how the authors have dealt with EU policies on the policy density for EU member countries. Please clarify.\n4. In the models displayed in Table 2, the authors never consider a full model (i.e. adding multiple variables into the model rather than just one variable at a time and then removing it again). This is especially odd as their individual models suggest that the additional variables matter – hence this is suggesting that each individual model (and the coefficients of the individual variables) suffer(s) from omitted variable bias. I would recommend to show a full model (at least adding the dummy variables if adding all HHI indicators does not make sense).\nMinor comments:\n5. In line 860 the authors state that the residuals are iid. Is this tested? Or assumed? Given the lack of testing for autocorrelation, cointegration and other common empirical issues, I would assume that this is their assumption (similar in S1 line 161).\n6. In their cumulative policy density measure, do the authors also account for discontinued policies (e.g. the Australian carbon pricing scheme that only ran for a few years)?\n7. In Figure 1, I’m unclear what the ranges left and right of the schematic mean. I would suggest to clarify this.\n8. In Table 2, I would recommend adding a row at the top with the dependent variable. From what I gather from the note below the table it is always the same (CO2 intensity) but the headings on first reading suggest they are different. I would suggest to add a row clarifying the dependent variable.\n9. Unless I have missed it, I would recommend to add specific equations and further explanation (including maybe examples) for the calculation of the HHI in the S1. This would help comprehension of the HHI variables.\n10. The two paragraphs between line 60 and 62 seem disjointed. I am unclear whether the studies cited in line 60 are supporting the statements in line 62, especially as they are not cited in that paragraph anymore.\n11. Line 73 suggests the authors have built the underlying policy database while in the methods it seems that the authors have used the existing Policies and Measures database from the IEA. Perhaps it would be good to clarify in the main text that additional analysis went into the database.\n12. In line 856 the subscript i should likely not be capitalised.", "reviewer_3": "The authors investigate the effectiveness of policies in reducing CO2 emissions. Based on a panel dataset of 43 countries 2000-2019, the authors test whether the number of policies, specialization on instrument types, sectoral coverage, emission reduction targets, and government institutions affect CO2 emission intensities.\nIn my opinion, this is a promising manuscript, to which I have the following comments to give:\n1. As the title and the beginning of the discussion rightly suggest, the ultimate goal of climate policy is to reduce the absolute level of emissions, not intensities. Accordingly, it would be critical for the authors to look at the level of emissions as outcome variable as well. This could contribute valuable insights into possible rebound effects of climate policies. If policies incentivize efficiency improvements, possibly in connection with an economic stimulus, policies could increase emissions despite relative decoupling of GDP from CO2 emissions. Also a possible interaction effect of policies and absolute targets on absolute emissions would be interesting to see. Any relatively time-invariant country characteristics (size, population, institutions, ...), that affect the average level of emissions and GDP, are absorbed by the unit fixed effects and are thus not a valid reason to only investigate intensities.\n2. While I think the fixed effects model specification generally is a good choice, the control variables could be problematic in the sense of \"bad control\". For instance, one way to achieve a lower GDP CO2 intensity is to shift economic activity to the service sector while offshoring polluting manufacturing. This means climate policies could affect both the control (service value added, imports, ...) and outcome variable (emissions). I would like to see a parsimonious specification (with only the fixed effects and policy measures) as a baseline and a more detailed discussion of possible mechanisms.\n3. The authors state that there are no significant differences between instrument types (regulatory, economic, voluntary) but I was not able to find the corresponding results. It would be surprising if voluntary instruments were as effective as mandatory types.\n4. How common is the exit of policies in the data? When governments change so often does their ideological stance. For instance, Trump tried to undo environmental policies of the Obama administration. Is this relevant for the results?"}, "author_response": ""}, {"round": 2, "reviewer_comments": {"reviewer_1": "The paper has improved a lot, and I think the paper presents interesting insights in the impact of policies. I think the authors have addressed the many comments in a good way with a very detailed response. Although for some comments they were not able to address those, but this was due to good reasons as they indicated.\nI think one of my main omission of the analysis was policy stringency is missing, because the number of policies is not a good measure of the quality and GHG impact of climate policies. The authors have included literature that showed that policy stringency and policy density are also strongly correlated, so I think well addressed.\nThe work is original, but soon after their submission Stechemesser et al. published a similar analysis in Science. I asked for a comparison with Stechemesser et al. , but I think this is still not done yet. In their response to my reviewer’s comments they mentioned that “Stechemesser et al identify total emission reductions in the range 0.6-1.8 GtCO2 from their set of 69 policy-attributed structural breaks in emission trends. This is an order of magnitude smaller than the estimate of 27.5 GtCO2 reductions in this study across all policy portfolios including continuously incremental reductions as well as major discontinuities.”\nI was surprised to see this difference. However, the authors did not discuss the much lower reduction found by Stechemesser et al in their paper.\nAction required: It would be good if the authors would discuss this major difference, and the possible reasons, as the reader may expect a comparison with Stechemesser et al., as this study has a similar research objective. The comparison could also move to the SI, and only highlight the main conclusions in the main text.", "reviewer_2": "I would like to thank the authors for their efforts in revising and improving this study. I feel that the study has substantially improved. I would like to highlight that the authors have considerably improved their discussions of endogeneity and attribution in the supplementary part of their paper. I think this discussion was necessary and has benefitted the overall paper.\nI appreciate the efforts by the authors to defend their attribution claims in the study and indeed I believe there is a good discussion (mainly the Granger causality testing) surrounding the temporal setting that policies are antecedent to emission reductions.\nHowever, I remain critical of the causal validity of the counterfactual construction and the headline number of cumulative reductions of 27 GtCO2. I do not believe that simple precedent from another study is enough to justify the term “attribution”. I remain partly convinced that the policy density measure is more a representation of how liberal a society is and how important climate change is for society – but I’d be very careful to translate their results into policy advice. Maximising policy density is clearly not what we should be doing – we should carefully design a small number of (mixed) effective policies with clear aims and effect pathways rather than aim to simply increase policy density.\nAt the very least, I would recommend to the authors to further review their language in lines 88, 100 and 295 and to directly compare their headline statements with Stechemesser et al. in the main text, as they do in at the bottom of page 4 of the rebuttal to reviewer 1.\nI would also suggest to clarify that their results do not challenge the validity of the Tinbergen rule – but rather that their results indicate that policy-makers are not actually adhering to it. As currently framed, they seem to suggest that their results show that the Tinbergen rule is not valid.\nI would further remove the implicit reference to the EKC in line 144 – there remains substantial academic debate around the presence of an EKC in carbon emissions, so I would rephrase that element.\nI recommend to avoid using the abbreviation “IV” in Table 1 for independent variables – this in econometrics generally refers to an instrumental variable and could be confusing.\nI would also ask the authors to show the full numbers in the two rightmost columns in Table Methods 2.", "reviewer_3": "The authors have responded to my comments and mostly implemented appropriate changes in the manuscript. I still have some major comments about the identification strategy and interpretation of results.\n1. The selection of control variables is not sufficiently justified and could substantially bias the coefficient of interest, yielding misleading results, even if well intentioned. In response to my previous concern about bad control, the authors provided to additional models ED16 in which they separately exclude the service and import shares. In SI1 Section 2.9, the authors state that the estimate of beta1 \"remains virtually unchanged\" when omitting these variables. This is true for the service share but without the import share the point estimate of beta1 decreases by 35% and notably increases in variance. In my opinion, this is a relevant change that suggests a mediating role of imports.\nA rigorous engagement with the functional relationships of the included variables is still missing, possibly in the form of a directed acyclic graph (Cinelli et al 2024). As parsimonious specification in a two-way fixed effects setting, I would expect models with only the explanatory variable of interest, especially since the FE already absorb a very large share of the total variance in the outcome (~70% in this case).\n1.1 There are some variables that are possible mediators, ie variables that could be affected by the treatment and in turn can affect the outcome, namely GDP, the service share, and the import share. I would like to see these variables regressed on policy density, including also lagged density since adjustment to supply chains and sectoral composition likely take several years. If policy density affects these variables, then they are bad controls, bias beta1, and should not be included (Angrist and Pischke 2009, Cinelli et al 2024).\n1.2 There are some variables which are basically time-invariant and are already accounted for by the unit FE, eg institutions. In that sense, the standard deviation reported in supplementary table 1 is misleading because it does not reflect the variance that is actually used to estimate the models. It would be helpful to report also the within SD here, ie the SD of the FE residuals (Mummolo and Peterson 2018). I would assume that almost all variance in the variables related to institutions and economic structure is absorbed by the FE.\n1.3 Temperature varies randomly, given the unit and time FE. Regressing temperature anomalies on policy density should yield an insignificant effect which might be a good placebo test. As such it is no confounder / omitted variable and it is neither necessary to include it as control nor does including it bias the estimate of beta1.\n1.4 Since no track changes are provided, it is not immediately obvious what the authors changed in the manuscript.\nHowever, I was not able to find any discussion of possible mediators in the main text (besides the moderating role of targets).\n2. Related to 1.2, in the current presentation of the results it is not clear how large the effect sizes are. Currently, the interpretation seems to be \"An increase in policy density by 1, decreases emissions intensity by 0.05%\". Is this a practically relevant effect size? Is a marginal change by 1 in policy density still plausible after partialing out the the FE? It would be very helpful to report also estimates that are standardized using the within SD as suggested by Mummolo and Peterson (2018). This way all variables would be on the same scale and the reader could easily assess the relevance of the effect sizes.\n2.1 In response to my previous comment, the authors provide interesting additional estimates by type of instrument in ED13. Here it is striking that the effect legal interventions is MUCH larger than any of the other types (eg 100 times larger than of market-based economic instruments). Some other instruments do not significantly affect CO2 intensity at all. This seems like the effect could be driven entirely by legal instruments. is this the case, ie is the coefficient still significant when omitting legal instruments from the policy density index?\n2.2 It would be less confusing to present the regression results in Table 1 in a standard format (models in columns, not rows). The caption should explain how to interpret the coefficients (as in line 663ff). Also it could be clarified here what is included in the 3 types and 8 types.\n3. The link to the replication materials does not work for me so I cannot comment on the availability of the materials."}, "author_response": "Climate policy portfolios that accelerate emission reductions\nRevised submission: Jan 2025\nResponse to Reviewers.\nWe respond in detail to all the reviewers’ comments below with a summary of the main changes\nin our revised submission. Prompted by the reviewers’ recommendations and concerns, we have\nboth extended the time frame of our analysis from 2019 to 2022, rerun all our models, and\nconducted new analyses along multiple dimensions including absolute emissions as dependent\nvariables, policy stringency indices, subsets of instrument type, alternative diversity indices, and\nboth full and more parsimonious model specifications. We have also conducted endogeneity and\ncausality tests to strengthen our attribution of emission intensity reductions to policy\naccumulation rather than vice versa. We have updated all figures and tables with these new\nresults, accompanied by full discussion in new sections of SI1, and summary explanations in main\ntext and Methods. The revised submission is significantly strengthened as a result, and we\nappreciate the reviewers for encouraging this.\nREVIEWER COMMENTS\nReviewer #1 (Remarks to the Author):\nR1.1 The study and its methodology are transparent and well written. I also like the\npresentation of national figures in the paper and the thorough analysis of national projections in\nthe supplementary information. The study finds quantitative evidence that national climate\npolicy portfolios that specialise in certain instrument types and sectors are associated with faster\nreductions in fossil CO2 emission intensity. The link with policy instruments is particularly\ninteresting. This study builds on the methodology of Eskander and Fankhauser (2020), but the\nauthors have extended it to a longer time horizon (2000-2019) and cover more policies. The in-\ndepth country analysis of this study is also an added value compared to the 2020 study. I think the\nwork could be important in this area, although a better presentation in a chart of the main\ninstrument types and sectors associated with faster reductions in fossil CO2 emission intensity for\na selected group of countries would be welcome. As it is, the main policies are included in the\nfigures, but this is widely known.\nResponse:\nWe tried lots of different figure options to combine the instrument types and sectors for select\ncountries with the vignettes on policy density & policy milestones against aggregate CO2/GDP\ntrends shown in our original Fig 2. All the options we tried became overly crowded with different\ndimensions in the data, so we have updated our original Fig 2 to the extended 2000-2022\ntimeframe, and included additional country Figs in SI2 visualising the complement data on\ninstrument type shares and sectoral coverage shares. We also provide the underlying data for all\ncountries (including those in the vignettes) in Table ED11. An example of these new country Figs\nin SI2 is shown here for the US.\nPolicies CO2 - Response to Reviewers 1\nFigure S4. Instrument types and changes in emission intensity per sector in the United States.\nNote: Based on policy data from the IEA Policies and Measures Database (PMD) and carbon emission data from the IEA\nCO2 Emissions From Fuel Combustion Database.\nMain changes in revised submission:\n- new Fig in SI2 with instrument type and sectoral shares\n- updated Fig2 in main text to 2022\nR1.2 The disadvantage of the method is that it still uses the period that is not very recent, as it\nmisses the last five years where even more policies have been developed, as we also see in the\nfigure, as it misses Fit-for-55 for the EU and IRA for the US. I can understand why you did not\nfocus on the period until 2022 because of the impact of COVID, but the current emissions trend\nfor some countries with many climate policies are lower compared to 2019 levels (Canada, US,\nEU).\nResponse:\nWe have updated all our independent, control and dependent variables to 2022, and re-run all our\nmodels (including additional robustness checks) for the period 2000-2022.\nPolicies CO2 - Response to Reviewers 2\n(Some of our independent and control variables - sectoral CO2 emissions and climate variability -\nare not yet available for 2023 so we were unable to include this additional year, except in lagged\nmodels of our dependent variable CO2/GDP).\nAll our findings reported originally for the period 2000-2019 hold in the extended model for\n2000-2022. In some cases our original findings are strengthened as the reviewer suggested given\nrecent climate policy activity in the US and elsewhere. Indeed, extending the policy count time\nseries sees the US overtake China for the largest number of policies in 2022, capturing the IRA-\nrelated policy activity under the Biden presidency. 41 instruments in our extended policy\ninstrument database are directly linked to the IRA (see also IEA policy report here). The effect of\nthe EU’s Fit-for-55 strategy is also evident but less marked - we think because it was proposed in\n2021 but not passed till 2023, and was also a more cumulative strengthening of a large pre-\nexisting (prior to 2021) policy corpus in EU countries.\nIn the revised manuscript, we have updated all our model results (main text, methods, SI1,\nExtended Data tables) and our policy vignettes (main text, SI2) for the period 2000-2022. Our\nextended main model to 2022 now shows the cumulative CO2 emissions avoided from the\nadoption of all policy portfolios in our 43 country sample is 27.5 GtCO2 (up from 15.9 GtCO2 in\nour original model to 2019).\nCovid impact in 2020:\nThe major impact of Covid-related disruptions in 2020 (and to a lesser extent in 2021) affect both\ntotal CO2 emissions and GDP in our dependent variable, so our extended models are broadly\nrobust to the Covid discontinuity in emission trends.\nThe one exception is in our HHI diversity measure of policy sectoral coverage when this is\nweighted by sectoral emissions. In our original model to 2019, the emission-weighted HHI\ndiversity measure had a significant negative coefficient, in line with expectations: policy\nportfolios weighted towards high emitting sectors are more effective (ceteris paribus). In our\nextended model to 2022, this coefficient becomes non-significant. We think the reason is that the\nsectoral shares of emissions in 2020 deviates from the longer-term trend, for example, due to the\ndrop in transport sector emissions under lockdown-related travel restrictions. We include the\ncountry data for this effect in Table ED11. The main diversity index we used - the HHI - is\nsensitive by design to anomalous changes in sectoral shares. This causes the HHI diversity\nmeasure of emission-weighted policy sectoral coverage to drop in significance (shown in Table\nED3a).\nIn further robustness testing, we find that the alternative Shannon Index diversity measure which\nis less sensitive to anomalous changes in sectoral shares remains negative and statistically\nsignificant in both the original 2000-2019 model and the extended 2000-2022 model (shown in\nTable ED3b). We have included this as a new section of SI1.\nMain changes in revised submission:\n- all model results, tables, figures & policy vignettes updated for period 2000-2022\n- additional tests for effect of Covid 2020 anomaly in main text and Table ED3a (sectoral\ncoverage HHI for 2000-2019 for comparison) and Table ED11 (transport sector share of\nemissions pre- and during 2020).\nPolicies CO2 - Response to Reviewers 3\n- additional robustness test using alternative Shannon Index as a diversity measure in SI1\nand Table ED3b\nR1.3 There is also an interesting paper in Science on climate policies that have achieved large\nemission reductions: Global evidence from two decades, which looks at 1500 climate policies\nimplemented between 1998 and 2022 in 41 countries across six continents. It would be good if the\nauthors would also compare some of their results with this study, although I can understand that\nthis study was published after your submission.\nResponse:\nIndeed, the Stechemesser et al. paper came out in Science a few weeks after we submitted our\nmanuscript and is a clear new reference point in the policy attribution literature. They use a\ndifference-in-difference (DiD) approach to evaluate the effect of combinations of policies in 41\ncountries over the period 2000-2020. Their country sample and time period are very similar to\nours, but there are three important differences with their aim and methodology which mean our\nstudy is non-overlapping but strongly complementary.\nFirst, their aim is to evaluate policies responsible for major near-term reductions in emissions.\nConsequently their dependent variable is structural breaks - statistically identifiable\ndiscontinuities - in sectoral emission trends.\nSecond (and as a consequence of this aim), their methodology uses difference-in-differences\ntesting to attribute the discontinuity to specific combinations of policy instruments introduced or\ntightened in the preceding 2 years in the corresponding sector. The difference-in-differences\napproach allows them to demonstrate causality more robustly from policy instrument\ncombinations to discontinuous reductions in emissions. They find policy instruments as part of a\nmix are generally more effective than those implemented alone, pointing to the importance of\ncomplementarity in portfolio design. (Taxation is an exception that works well as a stand-alone\npolicy). They also find that effective policy mixes by country and by sector so caution against\none-size fits all prescriptions.\nIn contrast, our approach using fixed effect models fitted to panel data is designed to identify the\ncumulative (non-discontinuous) effect of national policy portfolios - as opposed to the discrete\nand immediate effect of specific policy instrument combinations in the specific cases they identify\nin which these cause major reductions in emissions. So whereas Stechemesser et al. evaluate the\nnear-term effect of particular combinations of sectoral policy in 69 specific cases of emission\ndiscontinuity, our approach evaluates the longer-term effect of policy portfolios in general cases\nof emission reduction trends.\nThis cumulative focus of our approach using national policy portfolios also allows us to test and\ndemonstrate the interacting effect of framework targets and organisations that play out over the\nlonger-term. This is a further complementary novelty of our work alongside Stechemesser et al.\nIt is interesting to note that they identify total emission reductions in the range 0.6-1.8 GtCO2\nfrom their set of 69 policy-attributed structural breaks in emission trends. This is an order of\nmagnitude smaller than our estimate of 27.5 GtCO2 reductions across all policy portfolios\nincluding continuously incremental reductions as well as major discontinuities. This points to the\nPolicies CO2 - Response to Reviewers 4\nimportance of combining both approaches to policy attribution capturing both ‘big bang for your\nbuck’ immediate effects of specific policy combinations and ‘slow burn’ cumulative effects of\npolicy portfolios.\nIn this context, we also note that policy evaluation studies are designed to identify ex post the\neffect of specific policies on emission reductions as well as other policy objectives. We refer to\nthese in our discussion section. We have extended this discussion to include a new paper by\nDöbbeling-Hildebrandt et al. published in Nature Communications after we had submitted our\noriginal manuscript. They meta-analyse 80 ex post evaluation studies of 21 carbon pricing\nschemes worldwide to generalise the (de-biased) effect of this specific type of policy instrument to\nthe order of -4% to -15% emission reductions.\nMain changes in revised submission:\n- updated literature review (intro & discussion), with links to Stechemesser et al. findings\non on policy mixes, and on sector-specific policy combinations, and with links to\nDöbbeling-Hildebrandt et al. findings on evaluating specific policies\nStechemesser, A., N. Koch, E. Mark, E. Dilger, P. Klösel, L. Menicacci, D. Nachtigall, F. Pretis, N. Ritter, M. Schwarz, H.\nVossen and A. Wenzel (2024). \"Climate policies that achieved major emission reductions: Global evidence from two\ndecades.\" Science 385(6711): 884-892. doi:10.1126/science.adl6547\nDöbbeling-Hildebrandt, N., K. Miersch, T. M. Khanna, M. Bachelet, S. B. Bruns, M. Callaghan, O. Edenhofer, C.\nFlachsland, P. M. Forster, M. Kalkuhl, N. Koch, W. F. Lamb, N. Ohlendorf, J. C. Steckel and J. C. Minx (2024).\n\"Systematic review and meta-analysis of ex-post evaluations on the effectiveness of carbon pricing.\" Nature\nCommunications 15(1): 4147. 10.1038/s41467-024-48512-w\nI would recommend publication if the authors adequately address the main comments listed\nbelow:\nR1.4 The main difficulty I have is with the intensity of climate policy: It is obviously difficult\nto measure the stringency and GHG reduction impact of all types of climate policies.\nNevertheless, the lack of a measure of policy stringency is a major limitation of this paper,\nbecause the number of policies is not a good measure of the quality and GHG impact of climate\npolicies. Countries may have many policies and a high policy density, but this does not guarantee\nthat they will reduce CO2 emissions. For example, a single strong national policy based on an ETS\nwith nationwide coverage of all GHGs could be much more effective than multiple policies that\nhave not reduced emissions at all in the end. It all depends on the quality and stringency of the\npolicies and their coverage across sectors to determine the GHG impact. I therefore suggest that\nthe issue of stringency and the GHG impact of policies should be addressed in some way. I assume\nthat the earlier work by Eskander and Fankhauser also addressed this issue.\nResponse:\nWe agree that not accounting for policy stringency is an important omission. The Eskander &\nFankhauser paper on which we build also did not account for policy stringency. We had noted\nthe importance of further work on stringency in the discussion of our original manuscript, but we\nappreciate the reviewer pushing us on this as we have been able to make progress using an OECD\ndataset.\nPolicies CO2 - Response to Reviewers 5\nQuantitative stringency measures are not commonly compiled due to difficulties in standardising\nstringency assessments across heterogeneous policy contexts. To the extent they are available, this\nis typically only for particular instruments, particularly carbon pricing for which the effective\n$/tCO2 price is a comparable measure across jurisdictions and pricing instruments including taxes\nand emissions trading schemes (World Bank 2023, see also\nhttps://carbonpricingdashboard.worldbank.org; and an alternative ‘Real Carbon Price Index’\npublished by Monash University, see also https://www.realcarbonindex.org/indices).\nThe only measure of policy stringency we could find is the OECD Climate Actions and Policies\nMeasurement Framework (CAPMF) by Nachtigall et al. (2022). CAPMF provides one index on\nthe stringency of climate policies, with sectoral sub-indices (including for buildings, industry,\ntransport, and electricity supply). The index measures the degree to which sectoral climate\nactions and policies incentivise or enable GHG emissions mitigation.\nThe timeframe of the CAPMF is 1990-2022, matching our extended model period, but the OECD\ncountry sample does not include Brazil and the United States. Additionally, the policies covered\nby CAPMF do not include many of those coded as ‘voluntary’ or informational in our sample.\nPolicy stringency and policy density are also strongly correlated. This was demonstrated by\nSchaffrin (2015) with their novel measure of policy ‘strictness’ for three countries’ climate\npolicies. The OECD have recently confirmed this with the CAPMF as their own stringency\nmeasure - see, for example, Fig 3.2 in the OECD’s report on CAPMF (Nachtigall et al. 2022). As a\ncountry example for the UK, Fig 3.5 shows that stringency increased with the adoption of more\npolicies over time. The policy density variable in our sample without US and Brazil has a 71%\ncorrelation with the CAPMF.\nSo for these three reasons - correlation with policy density, mismatch in policy instrument scope\n(misspecification), mismatch in geographic scope - we limit our use of CAPMF to robustness\ntesting our main models (reported in SI1 and referred to in main text and methods).\nAs we cannot include the policy stringency index in our models alongside policy density due to\ncollinearity, we use the OECD CAMPF as an alternative independent variable. Specifically, we\ntake the mean of the sectoral policy stringency indices from CAMPF weighted by each sector’s\nshare of total emissions. (This is similar to our procedure in constructing emission-weighted\ndiversity indices in our testing of policy sectoral coverage).\nWe show the full results in Table ED12. Like policy density, the coefficient for the weighted\nsectoral policy stringency index is negative and statistically significant at p<.01. This shows that a\nmore stringent climate policy corpus is associated with faster reductions in emissions intensity.\nDespite the limitations noted for the stringency index including its exclusion of voluntary\ninstruments as well as Brazil and the United States, we find it performs very well, offering\ncomplementary insights to our main finding on the effect of climate policy density on emission\nintensity.\nMain changes in revised submission:\n- new SI1 on policy stringency model with links to full model results in Table ED12\nPolicies CO2 - Response to Reviewers 6\n- summary of findings and revised discussion in main text\nIEA (2024). Energy Efficiency 2023. Paris, France, International Energy Agency.\nNachtigall, D., Lutz, L., Rodríguez, M. C., Haščič, I., & Pizarro, R. (2022). The climate actions and policies measurement\nframework: A structured and harmonised climate policy database to monitor countries' mitigation action. (OECD\nEnvironment Working Papers, Issue No. 203). https://doi.org/10.1787/2caa60ce-en\nSchaffrin, A., S. Sewerin and S. Seubert (2015). \"Toward a Comparative Measure of Climate Policy Output.\" Policy\nStudies Journal 43(2): 257-282. https://doi.org/10.1111/psj.12095\nWorld Bank (2023). State and Trends of Carbon Pricing 2023. Washington, DC, World Bank.\nhttp://hdl.handle.net/10986/39796\nR1.5 I also don't quite understand why the authors use policy intensity in terms of numbers,\nas this does not take into account total GHG emissions, nor sectoral coverage, and compare it to a\ncountry's emissions intensity (i.e. nationwide emissions). I would expect policy density to also be\nrelative to the size of a country's emissions, as well as sectoral coverage. Perhaps you could\nelaborate on this.\nResponse:\nWe follow the precedent of Eskander & Fankhauser (2020) in using policy density (cumulative\ntotal number of policies) as our main independent variable, building off wider political science\nliterature on policy density (Shaffrin 2015) as well as studies of policy accumulation and policy\nsequencing (Pahle et al. 2018, Nascimiento et al. 2023). This literature emphasises policy density\nas a useful measure for explaining variation in countries’ progress in reducing emissions over time.\nBy using CO2/GDP rather than absolute CO2 emissions as our dependent variable, we also\naccount for variation in economic performance and country size - although in terms of the\neconomy rather than emissions. In response to the reviewer’s concern, we ran new models with\nabsolute fossil CO2 emissions as the dependent variable, with controls to account for variation in\ncountries’ development stage. For this, standard controls are log GDP per capita and its\ninteraction with the square term (as the relationship between development stage and emissions is\nnon-linear), but we also ran additional models with log GDP or log population as direct controls\nof country size. These new model results are reported in full in Table ED15, and are in line with\nexpectations: higher policy densities are associated with faster reductions in CO2 emissions,\ncontrolling for variation in country size and development stage. (For full discussion of these\nresults with CO2 emissions as the dependent variable, see R3.2).\nIn terms of sectoral coverage, all 43 countries in our sample have policies targeting emissions in\nall six emitting sectors. We show the sectoral share data in full in Table ED11. (There are two\nexceptions: Iceland has no climate policies in the energy industry sector; Switzerland has no\nclimate policies in the agricultural sector). So it’s not possible to weight policy density by sectoral\ncoverage. However, we do account for the concentration of policies on higher emitting sectors in\nour emissions-weighted diversity measure of policy sectoral coverage. As the reviewer suggests,\nnational policy portfolios concentrated on sectors accounting for a higher share of total emissions\nare associated with faster reductions in emission intensity. These model results are reported in full\nin full in Tables ED3a and ED3b, and summarised in the main text and methods.\nPolicies CO2 - Response to Reviewers 7\nTo test this sectoral effect further in response to the reviewer’s concern, we ran further models\nfor each sector (except energy industry) using sectoral CO2 emissions normalised by total GDP as\nthe dependent variable, and sectoral policy counts as the independent variable. For each model,\nwe also test sectoral policy stringency (using the sectoral CAMPF index) as an alternative\nindependent variable - see response R1.4 for details on the CAMPF). This approach is limited in\nthat the GDP normalisation is for the whole economy not the sector (for which sufficient time\nseries data were not available to match our country x time panel). However, all the sectoral model\nresults show negative and significant coefficients for policy density and for the alternative policy\nstringency variable as expected, and consistent with the main economy-wide results. The one\nexception is that policy density in the buildings sector model is negative but not significant. As\nthe alternative specification using policy stringency does show a significant coefficient, we think\nthis exception is a model artefact due to reduced heterogeneity as some smaller countries have\nvery few buildings sector policies. We report these sectoral model results in full in Table ED18.\nWe also interpret the reviewer’s concern as being about endogeneity - that higher emissions lead\nto more policies (in order to tackle those emissions). We respond in detail to endogeneity\nconcerns in R2.1 below. A summary of our response is that we combine lagged models, new\nendogeneity and causality tests, model selection, and grounding in literature to substantiate our\narguments that policy density drives reductions in emission intensity, not the other way round.\nHowever, with our fixed effect panel model we are unable to conclusively rule out endogeneity\nconcerns. (See R2.1 for full discussion).\nMain changes in revised submission:\n- new model results for absolute CO2 emissions as dependent variable in Table ED15,\nwith\nnew section in SI1 discussing the results\n- new model results for sectoral policies in Table ED18, with summary of findings and links\nto model results in Methods and SI1\nEskander, S. M. S. U., & Fankhauser, S. (2020). Reduction in greenhouse gas emissions from national climate legislation.\nNature Climate Change, 10(8), 750-756. https://doi.org/10.1038/s41558-020-0831-z\nNascimento, L., M. den Elzen, T. Kuramochi, S. Woollands, I. Dafnomilis, M. Moisio, M. Roelfsema, N. Forsell and Z.\nAraujo Gutierrez (2023). \"Comparing the Sequence of Climate Change Mitigation Targets and Policies in Major\nEmitting Economies.\" Journal of Comparative Policy Analysis: Research and Practice: 1-18.\n10.1080/13876988.2023.2255151\nPahle, M., D. Burtraw, C. Flachsland, N. Kelsey, E. Biber, J. Meckling, O. Edenhofer and J. Zysman (2018). \"Sequencing\nto ratchet up climate policy stringency.\" Nature Climate Change 8(10): 861-867. 10.1038/s41558-018-0287-6\nSchaffrin, A., S. Sewerin and S. Seubert (2015). \"Toward a Comparative Measure of Climate Policy Output.\" Policy\nStudies Journal 43(2): 257-282. https://doi.org/10.1111/psj.12095\nR1.6 I think the two tables are not always very attractive to the Nature Communications\naudience, especially those with many blank cells. A better presentation of Table 2 would be\nwelcome.\nResponse:\nPolicies CO2 - Response to Reviewers 8\nWe have moved the original Table 1 with the descriptive statistics for the variables in our model\nto the Methods section as Methods Table 1. We think it’s important to keep this table visible as\nthe underlying basis for our model results, even though it’s not the most attractive.\nWe have revised the original Table 2 with our model results to remove the blank spaces, though\nour previous format followed the convention when reporting econometric model results. We\nhope the reviewer agrees this new format is visually more acceptable. The revised table is now\nTable 1 in the main text.\nMain changes in revised submission:\n- original Table 1 descriptive statistics moved to Methods\n- new format for original Table 2 model results\nR1.7 It would also be good if the authors could present the most effective policies according to\ntheir analysis for the major emitting countries.\nResponse:\nOur study aim and approach is concerned with the cumulative effect of climate policy portfolios,\nincluding through the interaction with targets and governmental organisations. Although our\nmodels report clear and strong findings in each of these aspects, our approach is not designed to\nidentify the most effective policies within each national portfolio.\nThis would require a difference-in-difference (DiD) method in which each policy is analysed as a\ndiscrete intervention causing emissions to diverge from counterfactual without-intervention\ntrends. Indeed this is the method used by Stechemesser et al. in their recent Science paper for a\nset of 69 cases in which they had identified structural breaks in emission trends. From there they\nused DiD methods to identify which policies or combinations of policies in the previous 2 years\ncould be attributed as causing the break (see R1.1 for full discussion). Similar approaches using\nDiD are used in policy evaluation studies, but focused on specific policy interventions which are\nthe instrumental variable necessary for DiD. However, these methods would not be consistent\nwith our study aim.\nOur detailed policy vignettes for select countries provide a narrative account of policy\naccumulation that include discussions of effectiveness given each country’s institutional context,\nbased on literature. (The vignettes are summarised in Fig 3 in main text, and shown in full in SI2,\nupdated to 2022 in this revised submission). However, we are reluctant to use these narratives to\nmake strong claims about specific policies which we can not support in our modelling.\nIn our response to R3.6, we explain in full how we ran additional models for policy density by\ninstrument type in order to see whether we could identify which instrument type was more\neffective in general terms (as opposed to in specific countries). We ran a separate model including\ncontrols for policies coded in 1 of the 8 instrument types:\n- regulatory: legal interventions, monitoring, and regulations\n- economic: market-based and direct provision\n- voluntary: planning, informational, and other voluntary\nPolicies CO2 - Response to Reviewers 9\nFull results are shown in Table ED13. Given that our dependent variable is emissions intensity\n(CO2/GDP), we did not expect to find a clear effect given we were including as our independent\nvariable only a subset of all policies (coded as being of a particular instrument type). However, 5\nof the 8 models did show negative and significant coefficients for the policy density by\ninstrument type variable, with the largest coefficient in absolute magnitude being for legal\ninterventions and monitoring, both of which are categorised as ‘regulatory’.\nHowever, given the general limitation of these models including only a subset of policies in trying\nto explain economy-wide emission intensity, we are reluctant to over-interpret this result.\nMain changes in revised submission:\n- new model results for policy density by instrument type in Table ED13\n- clarifying text in Methods and discussion on study aim and limited ability to evaluate\neffectiveness of specific policy instruments in specific countries\nR1.8 Please use the Nature communications citation and references format.\nAddressed in the revised submission.\nSpecific comments:\nR1.9 You mention twice: \"National climate policy portfolios that specialise in certain types of\ninstruments and sectors are associated with faster reductions ...\". It would be good to give an\nexample of what you mean by certain?\nResponse:\nThis was unclear wording on our part which we have corrected. Our model results using diversity\nmeasures of policy sectoral coverage and policy instrument type as additional independent\nvariables alongside policy density show that in both cases specialisation (the opposite of\ndiversification) is associated with faster reductions in emission intensity. This general finding\nholds across our 43 country panel over the extended 2000-2022 time period. Our emission-\nweighted models of policy sectoral coverage do show that policy portfolios weighted towards\nhigher emitting sectors are in general more effective, but which sector these are varies by country\nand over time. In our additional testing of policy density by specific instrument types (see R1.7\nabove), we also show that legal, monitoring, and economic instruments are associated with\nreductions in emission intensity but we are reluctant to over-interpret these results given the\nlimitations of explaining economy-wide emission trends using only a subset of policies.\nOur study aim and modelling approach (discussed in detail in R1.3 and R1.7) mean we cannot\nspecify further which instrument types or which sectoral coverage are most effective. This will\nvary by policy tradition and emission profile in each country, and is the focus of policy evaluation\nstudies using a different methodology designed to answer this question - with the recent\nStechemesser et al. paper an excellent example (see R1.3).\nMain changes in revised submission:\n- rewording of findings on specialisation to avoid misinterpretation\nPolicies CO2 - Response to Reviewers 10\nPolicies CO2 - Response to Reviewers 11\nReviewer #2 (Remarks to the Author):\nR2.0 I would like to thank the authors for a very interesting and timely study on a very\nimportant topic. The question of the impact of individual policies and policies cumulatively is\nhighly relevant and hence deserves academic attention. I have a number of concerns that I would\nask the authors to address. Major comments:\nR2.1 My main concern about this study is the lack of discussion surrounding causal inference\nand endogeneity. The paper does not feature a discussion of the basis for the causal inference used\nin the paper. Are the authors claiming that the policy density is plausibly exogenous? Does the\npaper claim causality (and how would one avoid claims of reverse causality with higher emissions\nincreasing pressures on governments and then leading to more policies)? Or is this a descriptive\nassessment? This is especially relevant for wording such as “attributing” different effects as well as\nfor the headline statements that claim that those policies have reduced emissions by such a huge\namount. Could those policies be correlated with general economic development or other variables\nand dynamics? Furthermore, a number of co-variates are likely to be highly correlated (see\ndiscussion below with regards to the Energy Ministerial), which is also not discussed. I would\nexpect the authors to discuss questions like these explicitly and to clarify the causality basis that\nthey are making their claims by.\nResponse:\nOn wording, we agree it is ambitious to claim causality and we have made sure we do not do this\nin the revised submission. Generally we frame our analysis as showing associations between\npolicy portfolio variables and emission intensity reductions, with literature supporting the\ninference that policies are antecedent. However we recognise that the term ‘attribution’ - the\nfield of climate policy science to which our study contributes - does also imply causation. In the\napplied economics and political science literature, causal claims are only possible with Difference-\nin-Differences (DiD) methods which we discuss in R1.3 with reference to a recent Science paper\nusing this approach. In our work, we follow precedent (e.g., Eskander & Fankauser 2020) in\npositioning our approach as an attribution study.\nWe have multiple lines of reasoning to support our attribution of emission intensity reductions to\naccumulating policy density rather than vice versa: (1) lagged models, (2) endogeneity tests,\n(3) Granger non-causality tests, (4) fixed effects, (5) weak correlations with covariates, (6) supporting\nliterature and policy vignettes, (7) our choice of econometric model. We discuss each in turn.\n(1) Lagged models: We examine the lagged effect of policy density on emission intensity. A\nsignificant lagged effect indicates that an increase in the stock of policies drives emission intensity\nreduction, rather than the reverse. We report a 3 year lagged model in Table ED2 showing a\nnegative and significant coefficient for the policy density variable in line with expectations. We\nget broadly similar results for 1, 2, and 4 year lags.\nHowever, we recognise that policy density does not change much over some time periods in some\ncountries, so the lagged policy density variable could absorb the effects of other variables. In a\nfurther model reported in Table ED8 we include a 1 year lag on all controls as well as the policy\ndensity variable. Below we show that our controls are only weakly correlated with our policy\ndensity variable.\nPolicies CO2 - Response to Reviewers 12\n(2) Endogeneity tests: We ran standard endogeneity tests used in applied econometrics,\nspecifically the Durbin-Wu-Hausman test, following Wooldridge (2003, p. 483-484). Full results\nare included in a new section of SI1 with model results in Table ED14.\nAs an instrument for policy density, we use the sectoral stringency index (OECD CAPMF\ndiscussed in full in R1.4) which we know from literature controls for a similar effect to policy\ndensity on emission intensity, also indicated by the high correlation between the two variables\n(71%) in our panel.\nWe start with the baseline regression model B1 (column 1, Table ED14) then run model B2\ncolumn 2, Table ED14) in which emission intensity is replaced by policy density as the dependent\nvariable, while simultaneously introducing the OECD CAMPF sectoral stringency index as an\nindependent variable. We save the residuals from model B2 and add them in the baseline\nregression model (B3, column 3, in Table ED14) as an additional regression, where we observe\nthat the coefficient for the model B2 residuals does not reject the null hypothesis that the\ncoefficient δ=0. As a final test, we perform an F-test on the coefficient for the model B2 residuals\nthat fails to reject the null. This further shows that the specific regressor is not endogenous, giving\nus further evidence to reject the reverse causal explanation that emission intensity results in\nhigher policy density.\nWe summarise these results here, and refer the reviewer to Table ED14 for the full models with\ncontrols.\nSummary of Table ED14. Durbin-Wu-Hausman endogeneity test for policy density.\nModel B1 Model B2 Model B3\nLog(CO2/GDP) Policy density LOG(CO2/GDP)\nPolicy density -0.000555*** -0.000436\n(0.000169) (0.000569)\nStringency index 15.59***\n(1.387)\nModel B2 residuals 9.38e-06\n(0.000617)\nControls YES YES YES\nObservations 941 898 898\nWithin R-squared 0.2729 0.3113 0.273\n*** denotes statistical significance at 1%, ** at 5%, and * at 10%. Parentheses indicate standard errors for\neach coefficient.\n(3) Granger non-causality tests: As an additional sensitivity analysis of the relationship between\ntotal policy density and emission intensity, we specify Granger non-causality following\nDumitrescu and Hurlin (2012). Results in the Table below show that the null hypothesis of\nGranger non-causality is rejected at 1% statistical significance level, a result that holds when we\nadd a lag operator of order 3.\nSummary Table of Dumitrescu-Hurlin (2012) test on whether policy density Granger-causes\nemission intensity reduction.\nLag 0 Lag 3\nPolicies CO2 - Response to Reviewers 13\nW-stat Zbar-stat P-value W-stat Zbar-stat P-value\nPolicy density 6.5810 25.8779 0.0000 10.3218 19.6010 0.0000\nNotes: Null hypothesis that policy density does not Granger-cause reduction in the natural logarithm of\nemissions intensity. Rejection of the null indicates there is Granger causality.\nWe note that although the Dumitrescu-Hurlin test, like most statistical tests of causality, is useful\nfor detecting potential temporal causal relationships between independent and dependent\nvariables, it has limitations in establishing reverse causality for which arguments based on prior\nhypotheses and causal reasoning are important.\n(4) Fixed effects: Empirically, policy density is affected by differing policy traditions across\ncountries, which is captured in our models by the country fixed effects. Policy density also\nincreases over time (shown in our SI1 plots per country) due to increasing issue salience and\nprioritisation as well as secular trends (e.g. economic development and strengthening policy\ncapacity). This is captured in our models by year fixed effects. Both these model features help to\navoid our findings being the result of spurious correlations.\n(5) Weak correlation between co-variates: There is generally low or very low correlation between\npolicy density and the control variables used in our models over the period 2000-2022. The\nhighest correlation is 22.8% for services share of GDP; all others are below 20% (temperature\nvariation 19.5%, imports share of GDP -16.6%, GDPpercap log 14.0%, rule of law 0.08%,\nHodrick-Prescott GDP filter -0.01%). These are all substantially lower than the correlation with\nthe OECD CAMPF sectoral stringency index (71%), which we use as an instrument to test for\nendogeneity. In general we find that policy stocks are not correlated with general economic\ndevelopment or other variables and dynamics.\nWe address correlation between policy density and our governmental organisation dummy\nvariables including CEM in more detail in Response 2.2 below.\n(6) Supporting literature and policy vignettes: Consistent with the literature, we are confident\nthat policy density is indeed plausibly exogenous, and that our analysis goes beyond a descriptive\nassessment.\nAll the climate policy portfolio elements we include in our models are designed to reduce\nemissions in line with policy priorities post-Kyoto Protocol (1997) in many OECD countries and\npost-Paris Agreement 2015) in all OECD+BRIICS countries.\nOur policy vignettes (see SI2) indicate that the implementation of new policies increasing the\ntotal stock is clearly antecedent to observed emission intensity reductions, rather than the other\nway round.\nStechenesser et al (2024) use DiD methods to show that combinations of policies lead to\ndiscontinuous reductions in sectoral emissions within two years of introduction. This shows\ncausality from policies to emission reductions.\nLike Eskander and Fankhauser (2020), our aim is different in assessing the path dependent effect\nof climate policy stocks on cumulative incremental emission reductions (with our additional\ntesting of the interacting role of long-term targets and governmental organisations). We align\nwith the methodological framework established by Eskander and Frankauser (2020) in the climate\nPolicies CO2 - Response to Reviewers 14\nattribution literature, and in our Methods and SI1 we show how we replicate their model\nspecifications for comparison.\n(7) Our choice of econometric model: Our choice of the two-way fixed effects (TWFE) estimator\nis grounded in evidence from the applied econometrics literature, that emphasises its capability in\nestablishing causality. Influential studies, such as Angrist and Pischke (2009) in applied\neconomics and Imai and Kim (2019) in political science, underscore the effectiveness of fixed\neffects models for identifying causal relationships in panel data. Millimet and Bellemare (2023)\nand Wooldridge (2021) provide a comprehensive overview of the econometric properties of the\nTWFE estimator, elaborating on its strengths and limitations in the context of causal inference\nwith panel datasets.\nWe make these arguments to support our decision to use the TWFE estimator, incorporating\ncross-sectional and time dummies, given our study aim of assessing the overall impact of policy\ndensity on emission intensity. With all the controls in our model, we are confident the estimated\neffect on emission intensity is clearly attributable to changes in policy density.\nAs noted, the main alternative method which allows for robust causal claims is the Difference-in-\nDifference (DiD) model (Baker et al, 2022). As in the Stechemesser et al. 2024 study discussed in\nR1.3, the DiD approach allows researchers to estimate the average treatment effect by comparing\noutcomes between a control group and a treatment group subject to a distinct policy intervention.\nHowever, given we examine the effect of accumulating policy stocks on emissions intensity, a\nsimilar approach focusing on distinct individual policies would not work. Directly comparing\nindividual policies across countries would invoke concerns over robustness, given the\nfundamental differences in the policies’ design, which are tailored to each country’s specific\ncharacteristics and needs. Such comparisons would fall under the umbrella term of ‘bad\ncomparison’ in which dissimilar policies are evaluated against each other. Baker et al. (2022) argue\nthat when staggered timing of treatment effects (i.e. policies introduced at different dates) is\ncombined with treatment effect heterogeneity (i.e. varying types of policies across different\ncountries), DiD estimates become biased and consequently misleading. This is particularly true in\nthe case of dynamic treatment effects (Sun and Abraham, 2021). For these reasons we do not\nconsider DiD methods appropriate for our research focus on cumulative national climate policy\nportfolios.\nIn sum:\nFrom these multiple arguments we are confident that both conceptually and methodologically\nour study goes beyond a descriptive analysis in being able to attribute emission intensity\nreductions to accumulating stocks of climate policies.\nMain changes to revised submission:\n- checked and removed any language on causation\n- clarification of reasons for claiming attribution (main text, Methods, and SI1)\n- new SI1 section on endogeneity & causality tests\nAngrist, J. D., & Pischke, J.-S. (2010). The Credibility Revolution in Empirical Economics: How Better Research Design\nIs Taking the Con out of Econometrics. Journal of Economic Perspectives, 24(2), 3–30. https://doi.org/10.1257/jep.24.2.3\nPolicies CO2 - Response to Reviewers 15\nBaker, A. C., Larcker, D. F., & Wang, C. C. Y. (2022). How much should we trust staggered difference-in-differences\nestimates? Journal of Financial Economics, 144(2), 370-395. https://doi.org/https://doi.org/10.1016/j.jfineco.2022.01.004\nDumitrescu, E.-I., & Hurlin, C. (2012). Testing for Granger non-causality in heterogeneous panels. Economic\nModelling, 29(4), 1450-1460. https://doi.org/https://doi.org/10.1016/j.econmod.2012.02.014\nEskander, S. M. S. U., & Fankhauser, S. (2020). Reduction in greenhouse gas emissions from national climate legislation.\nNature Climate Change, 10(8), 750-756. https://doi.org/10.1038/s41558-020-0831-z\nImai, K., & Kim, I. S. (2019). When Should We Use Unit Fixed Effects Regression Models for Causal Inference with\nLongitudinal Data? American Journal of Political Science, 63(2), 467-490.\nhttps://doi.org/https://doi.org/10.1111/ajps.12417\nMillimet, D., & Bellemare, M. F. (2021). Fixed Effects and Causal Inference. IZA Discussion Paper No. 16202.\nhttp://dx.doi.org/10.2139/ssrn.4467963\nNachtigall, D., Lutz, L., Rodríguez, M. C., Haščič, I., & Pizarro, R. (2022). The climate actions and policies measurement\nframework: A structured and harmonised climate policy database to monitor countries' mitigation action. (OECD\nEnvironment Working Papers, Issue No. 203). https://doi.org/10.1787/2caa60ce-en\nSun, L., & Abraham, S. (2021). Estimating dynamic treatment effects in event studies with heterogeneous treatment\neffects. Journal of Econometrics, 225(2), 175-199. https://doi.org/https://doi.org/10.1016/j.jeconom.2020.09.006\nWooldridge, J. M. (2021). Two-Way Fixed Effects, the Two-Way Mundlak Regression, and Difference-in-Differences\nEstimators. Available at SSRN: https://ssrn.com/abstract=3906345.\nWooldridge, J. M. (2003). Introductory Econometrics: A Modern Approach. (2nd Edition ed.). Cengage Learning.\nhttps://doi.org/https://doi.org/10.1198/jasa.2006.s154\nR2.2. I am highly sceptical about the results concerning the Clean Energy Ministerial as well as\nthe results concerning the presence of an energy ministry. The Clean Energy Ministerial is highly\ncorrelated with general institutions in a country (a government/society more focused on climate\npolicy is much more likely to sign up to this). Here, as above, causality is in my mind difficult to\nclaim – as even the direction of causality is unclear. Is the membership leading to more policy\ndiffusion or is policy knowledge in a government leading to joining such an institution? The CEM\nalso (in my experience) plays a negligible role in day-to-day policy-making but is often a publicity\nexercise.\nResponse:\nThis comment touches on several issues that warrant clarification. The first part refers to a\ncorrelation between general institutions in a country and CEM membership. It is true that CEM\nmembership is voluntary and as such no country is forced to join it. It is also true the CEM\nmembership indicates that climate action is considered salient in a country, but this is where the\npicture starts to become more nuanced.\nCountries choose to join the CEM for different reasons: some join because they are already\nactively adopting and implementing ambitious climate policies, and others join because they\nrecognise the need to do so (Tosun & Rinscheid, 2023). What the CEM does not accept is that its\nmembers make no effort to promote clean energy technologies. Becoming and remaining a\nmember of the CEM therefore requires a certain level of commitment. This commitment does not\nimply the adoption and implementation of common clean energy policies or the development of\nmore ambitious national policies. It means that countries participate in workstreams that they\nconsider relevant to their clean energy transition (Tosun et al., 2023). Some of the workstreams\nPolicies CO2 - Response to Reviewers 16\naim at improving the implementation (not the formulation) of domestic policies, but most of\nthem are designed to facilitate public-private collaboration in the diffusion of clean energy\ntechnologies that can contribute to reducing GHG emissions. \nAs an example the Transforming Solar workstream focuses on the solar PV manufacturing value\nchain and the development of resilient supply chain capacity and linkages among trading\npartners. Consequently, CEM membership provides access to collaborations aimed at stimulating\nthe diffusion of clean energy technologies that can help reduce GHG emissions (Carey and Yang,\n2023). This effect may be mediated through domestic climate or clean energy policies, but it may\nalso be a direct effect through technology diffusion.\nFor this reason, we consider it important to control for a potential effect of CEM membership in\nour models - not as a main effect but through an interaction effect with our main policy density\nvariable. These are the results we report.\nThe reviewer is right that we can not rule out reverse causality (discussed in detail in R2.1 above),\nbut by testing the interaction between CEM membership and policy accumulation we capture a\npathway to GHG emission intensity reduction that exists in addition to the policy pathway based\non the diffusion of clean energy technology.\nIn our original submission we were imprecise in this respect, and have clarified the text to refer to\nCEM’s role in clean energy technology diffusion. We fully agree with the reviewer that CEM\nmembership does not play a role in domestic policy formulation.\nGiven the reviewer’s concerns about our CEM results, we have also relegated them to SI1 and\nExtended Data Table ED5. In the revised submission, we include the IEA results in main text\n(Table 2) as IEA membership is more directly related to policy exchange and diffusion (see R2.4\nbelow).\nMain changes to revised submission:\n- removal of CEM interaction effect models from main text\n- clarification in main text on CEM role in clean energy technology diffusion (not policy\ndiffusion)\n- new section of SI1 with discussion of CEM role in clean energy technology diffusion\nTosun, J., & Rinscheid, A. (2023). What drives engagement in the Clean Energy Ministerial? An assessment of\ndomestic-level factors. Journal of European Public Policy, 30(3), 469-487.\nTosun, J., Heinz-Fischer, C., & Luo, R. (2023). Who takes the lead? A disaggregate analysis of the EU's engagement in\nthe Clean Energy Ministerial and Mission Innovation. Journal of Cleaner Production, 382, 135240.\nCarey, E., & Yang, X. (2023). From Paris to Glasgow and beyond: what future for clean energy technology deployment\nunder Article 6?. In A Research Agenda for Energy Politics (pp. 127-154). Edward Elgar Publishing.\nR2.3 I am highly sceptical about the results concerning the presence of an energy ministry. The\npresence of an energy ministry is arbitrary in my view. Every government (that I know of) has a\nministry dealing with energy issues, even if it is paired with other dossiers and independent of whether “Energy” appears in the name of a ministry (as I gather from their source Tosun 2018). This is also not a static component – consider for example the German vs the\nPolicies CO2 - Response to Reviewers 17\nUK case where in Germany the word “Energy” was dropped from the name of the department\nbecause climate was added to the ministries responsibility. In the UK Energy remained in the\nname, but the responsibilities of the ministries changed from BEIS, to DECC, to DENSZ – does\nGermany deal with Energy less than the UK? I am highly sceptical of those singular dummy\nvariables and would hence suggest to remove them (at the very least from the main text).\nResponse:\nThis comment is useful for explaining the nature of our dummy variable coding for energy\nministries and to elaborate on our rationale for including it in one of our models as an interaction\nwith policy density.\nFrom a theoretical viewpoint, the creation of dedicated ministries for certain policies is relevant\nfor our analysis in two ways as demonstrated empirically by Klüser (2023). First, the creation of\nan issue-specific ministry creates new bureaucratic capacity both to formulate policies that fall\nwithin the policy domain of a given ministry and to implement those policies. Second, the\ncreation of an issue-specific ministry indicates that an issue is salient to a particular government.\nIssue salience tends to vary over time. A strong indicator that the design of government ministries\nis influenced by issue salience is the change in their names. Our data on energy ministries vary\nover time and show that in some countries there were episodes when there was no ministry with\n“energy” in its name. It is true that “energy” is sometimes replaced by “climate”, “energy\nefficiency”, “energy security” or some other formulation, but this also reflects the salience of\nenergy-climate as a policy domain, both for formulation and implementation.\nFollowing Klüser (2023), dedicated “energy” or “climate” ministries increase the chances that\nformulated policies are fully implemented, and so increase the impact of policies on emissions.\nConversely, if a new government removes “energy” or “climate” from the name of a ministry this\nindicates a lower priority for the issue and is likely to reduce the capacity of the respective\nministry to formulate and implement policy which may weaken the effect of the policy corpus on\nemission reductions.\nTo better capture variation in ministry naming over time, including the German case mentioned\nby the reviewer, in our revised submission we have replaced the energy ministry dummy with an\nenergy and/or climate ministry dummy. This accounts for 50.6% of observations. We then reran\nthe models (extended to 2022) to test the interaction between this dummy and policy density. In\nline with our expectations, the interaction term was negative and significant.\nMain change in revised submission:\n- replacement of energy ministry dummy with energy and/or climate ministry dummy\n- rerun models with policy density X ministry interaction term - summarised in main text,\nand shown in full in Table ED5\nKlüser, K. J. (2022). From bureaucratic capacity to legislation: how ministerial resources shape governments’ policy-\nmaking capabilities. West European Politics, 46(2), 347-373. https://doi.org/10.1080/01402382.2022.2030602\nR2.4 The same applies to the IEA membership (especially the reverse causality argument) but it\nis more sensible than the other two.\nPolicies CO2 - Response to Reviewers 18\nResponse:\nThe 32 current member countries of the IEA are all in the OECD, so membership is an indirect\nmeasure of country development stage and income level, controlled for in our models by the GDP\nand GDP-squared terms. Originally the IEA was establish to represent the interests of oil-\nimporting countries (following the 1970s OPEC embargo) but has more recently been active in\npromoting pathways, policies, and clean energy innovation programmes in line with net-zero\ngoals (including through its hosting of the CEM; see R2.2).\nWe think it is legitimate to test whether IEA membership interacts with policy density for two\nreasons. First, the IEA has an explicit policy evaluation function in energy efficiency and demand,\nin clean energy innovation, in renewable energy and low-carbon technologies (e.g., country focus\nchapters in the annual Energy Efficiency and Energy Technology Perspectives reports). Second,\nthe IEA’s work aims to diffuse best practice policies and policy insights among its member\ncountries.\nOur modelling tests whether this interaction between IEA membership and accumulating policy\nstocks affects emission intensity reduction tests.\nAs with the CEM, the reviewer is right that we cannot rule out reverse causality - we discuss\ncausality and endogeneity in detail in R2.1 above.\nMain changes in revised submission:\n- inclusion of IEA interaction term model results in main text, with explanation of IEA role\nin policy diffusion\nR2.5 I notice that the authors have used a dummy for EU membership – but it is unclear to me\nhow the authors have dealt with EU policies on the policy density for EU member countries.\nPlease clarify.\nResponse:\nWe only consider national policies in our study. EU policies are not directly included in our\nmeasure of policy density. However, EU legislation is captured indirectly through the domestic\npolicies of EU member states when they transpose EU legislation into national law. This implies\nan interdependence between EU member states with regard to their climate policies (in addition\nto the many economic interdependencies), which we control for with our dummy for EU\nmembership. More specifically, this dummy also includes EFTA countries, which have to\ntranspose EU legislation, including climate policies, in order to be allowed to participate in the EU\nsingle market.\nMain changes in revised submission:\n- Clarification in Methods of how EU policies are coded in our main policy density variable.\nR2.6 In the models displayed in Table 2, the authors never consider a full model (i.e. adding\nmultiple variables into the model rather than just one variable at a time and then removing it\nagain). This is especially odd as their individual models suggest that the additional variables\nPolicies CO2 - Response to Reviewers 19\nmatter – hence this is suggesting that each individual model (and the coefficients of the individual\nvariables) suffer(s) from omitted variable bias. I would recommend to show a full model (at least\nadding the dummy variables if adding all HHI indicators does not make sense).\nResponse:\nIn our original work we had run full models as suggested by the reviewer, but we did not include\nthem in our original submission due to amplified collinearity problems with multiple\nindependent variables in the same model. This overspecification led to: unstable coefficient\nestimates and difficulty in determining the individual effects of each variable; loss of efficiency,\nreducing the precision of the estimated coefficients, and increasing standard errors; and\noverfitting.\nThis applies to the full set of policy variables (density, portfolios specialise on instrument type,\nportfolios concentrated on sectoral coverage) as well to the dummy variable for long-term targets\nand governmental organisational (energy and/or climate ministries, membership of CEM, IEA,\nEU-EFTA).\nWe also tried full models with all the dummy variable interaction terms (but not the additional\npolicy variables) together with our main policy density independent variable. As well as\ncollinearity problems, from an applied econometrics perspective, including all dummies and\ninteraction effects simultaneously in the same model specification makes the model practically\nuninterpretable as the dummies’ effects are interrelated.\nFollowing the reviewer’s recommendation, we ran further tests to see how complete we could get\nwithout compromising model quality and interpretability. In Table ED17, we report full\ncombined models with our main policy density variable, one of the four policy portfolio variables\n(instrument type and sectoral coverage), and five dummy variables - but no interaction terms - for\nlong-term targets (relative and absolute), for energy and/or climate ministries, and for IEA and\nEU-EFTA membership.\nAll coefficient signs and magnitudes are in line with those of the parsimonious models reported in\nTable 2 of the main text. Across all models, the coefficient for total policy density remains\nstrongly significant. The same holds for each of the policy portfolio variables that continue to\nperform well in their respective combined model. Significance of the energy and/or climate\nministry dummy drops away, as does the EU-EFTA membership (which is highly correlated with\nIEA membership).\nHowever, overall, these combined models give us further confidence in the results reported in\nmain text.\nMain changes in revised submission:\n- new full combine model results reported in Table ED17\n- new section of SI1 with discussion of full, combined model results, with summary in main\ntext\nMinor comments:\nPolicies CO2 - Response to Reviewers 20\nR2.7 In line 860 the authors state that the residuals are iid. Is this tested? Or assumed? Given\nthe lack of testing for autocorrelation, cointegration and other common empirical issues, I would\nassume that this is their assumption (similar in S1 line 161).\nResponse:\nCorrect, this is assumed. For transparency, we removed this statement from the main manuscript\nand SI1 and we now simply refer to 𝜀 as the regression residuals. Overall, Root Mean Square\n𝑖𝑡\nError (RMSE) estimates reported across model specifications in Table 1 (main manuscript) and\nExtended Data tables show minimal differences between predicted and observed values.\nR2.8 In their cumulative policy density measure, do the authors also account for discontinued\npolicies (e.g. the Australian carbon pricing scheme that only ran for a few years)?\nResponse:\nThe IEA Policies and Measures Database does not consistently report when policies end, so we\nwere unable to capture “discontinued” policies in our policy density measure.\nHowever, we believe this is not an issue for two reasons. First, the “discontinuing” or\n“dismantling” of policies is less frequent than one would expect. For example, Schaub et al. (2024)\nshow that only a small fraction of climate policies terminate over the course of time. Second, the\ndismantling of climate policies correlates with low adoption of new climate policies. So even if we\ndo not capture the dismantling of some policies during a period with a government with low\nclimate ambition, the effect of dismantling is included in the slow or negligible increase in policy\ndensity during this period.\nThe reviewer is right in pointing to the Australian case, where a change in government in 2013\nended the carbon pricing scheme. This dismantling of policies also coincided with few newly\nadopted climate policies. The figure below for AUT shows this inverse correlation between policy\nadoption and dismantling in Australia (taken from Figure S14 in the Supplementary File of\nSchaub et al., 2022).\nPolicies CO2 - Response to Reviewers 21\nIn another example, the first Trump administration dismantled climate policies while also\nadopting comparatively few new climate policies. This was in contrast to the previous Obama\nadministration and particularly the subsequent Biden administration.\nIn sum, our measure of policy density captures the comparatively rare occurrence of policy\ndismantling indirectly. Even if we could incorporate the dismantling of policies in our density\nmeasure, we would not expect our results to change significantly.\nMain changes in revised submission:\n- clarification in Methods of policy dismantling not being coded in our policy density\nvariable + explanatory text on the inverse correlation between dismantling and new\nadoption\nSchaub, S., Tosun, J., & Jordan, A. J. (2024). Climate action through policy expansion and/or dismantling: Country-\ncomparative Insights: An introduction to the Special Issue. Journal of Comparative Policy Analysis: Research and\nPractice, 26(3-4), 215-232.\nSchaub, S., Tosun, J., Jordan, A., & Enguer, J. (2022). Climate policy ambition: Exploring a policy density perspective.\nPolitics and Governance, 10(3), 226-238.\nR2.9 In Figure 1, I’m unclear what the ranges left and right of the schematic mean. I would\nsuggest to clarify this.\nResponse:\nPolicies CO2 - Response to Reviewers 22\nThe ranges in the schematic were supposed to indicate the variables we tested in our models;\nhowever we agree they were not clear so we have removed them. We explain the variables and\ntheir underlying measurements in detail in Methods and in SI.\nMain changes in revised submission:\n- revised Figure 1 in main text\nR2.10 In Table 2, I would recommend adding a row at the top with the dependent variable.\nFrom what I gather from the note below the table it is always the same (CO2 intensity) but the\nheadings on first reading suggest they are different. I would suggest to add a row clarifying the\ndependent variable.\nResponse:\nTable revised as suggested.\nR2.11 Unless I have missed it, I would recommend to add specific equations and further\nexplanation (including maybe examples) for the calculation of the HHI in the S1. This would help\ncomprehension of the HHI variables.\nResponse:\nFull equations and explanations of the HHI (and alternative Shannon Index) diversity measures\nincluded in SI1 as suggested.\nR2.12 The two paragraphs between line 60 and 62 seem disjointed. I am unclear whether the\nstudies cited in line 60 are supporting the statements in line 62, especially as they are not cited in\nthat paragraph anymore.\nResponse:\nWe have changed the text to clarify this. The ‘portfolio size matters’ was the simple summary of\nthe previous paragraph including its citations. The segue into the next paragraph shifts focus from\nnumbers of policies to portfolio design characteristics.\nR2.13 Line 73 suggests the authors have built the underlying policy database while in the\nmethods it seems that the authors have used the existing Policies and Measures database from the\nIEA. Perhaps it would be good to clarify in the main text that additional analysis went into the\ndatabase.\nResponse:\nWe have clarified in the main text on how we derived the policy data. We used the IEA Policies\nand Measures database as our data source. We then assigned the identified policies to sectors and\ninstrument types based on our own classification. And then we created our policy density\nmeasures. This involved transforming data at the policy level into aggregated data at the country\nyear level.\nR2.14 In line 856 the subscript i should likely not be capitalised.\nResponse:\nPolicies CO2 - Response to Reviewers 23\nWe couldn’t find this in our submission! We have checked all formulas and equations and think\nthey are all correct, but we will double check with the editorial team should the manuscript be\naccepted for publication.\nPolicies CO2 - Response to Reviewers 24\nReviewer #3 (Remarks to the Author):\nR3.1 The authors investigate the effectiveness of policies in reducing CO2 emissions. Based on\na panel dataset of 43 countries 2000-2019, the authors test whether the number of policies,\nspecialization on instrument types, sectoral coverage, emission reduction targets, and government\ninstitutions affect CO2 emission intensities. In my opinion, this is a promising manuscript, to\nwhich I have the following comments to give:\n[Authors’ note: we have moved R3.4 up to here, as we respond to R3.2 + R3.4 together]\nR3.2 As the title and the beginning of the discussion rightly suggest, the ultimate goal of\nclimate policy is to reduce the absolute level of emissions, not intensities. Accordingly, it would\nbe critical for the authors to look at the level of emissions as outcome variable as well.\nR3.4 Also a possible interaction effect of policies and absolute targets on absolute emissions\nwould be interesting to see. Any relatively time-invariant country characteristics (size,\npopulation, institutions, ...), that affect the average level of emissions and GDP, are absorbed by\nthe unit fixed effects and are thus not a valid reason to only investigate intensities.\nResponse:\nWe agree that ultimately climate policy has to reduce absolute levels of emissions. We use\nemission intensity as our dependent variable following the precedent in similar attribution studies\n(e.g., Eskander and Fankhauser 2020) because it accounts for changes in emissions driven by a\ncountry’s overall economic performance and size. (GDP and CO2 are correlated at 92% in our\nsample). Using emission intensity rather than absolute emissions therefore helps reduce\nconfounding factors when interpreting the effect of climate policy.\nIn response to the reviewer’s comment, we ran additional models reported in full in Table ED15\nand summarised in SI1 for which we use the natural logarithm of absolute CO2 emissions as the\ndependent variable instead of emissions intensity. Overall, results remain consistent.\nWe start by comparing our baseline model (column 1, Table ED15) with a new model\nspecification with ln CO2 as the dependent variable (column 2, Table ED15). The independent\nand control variables remain the same across both models. Policy density remains negative and\nstatistically significant with a smaller (in absolute terms) coefficient compared to the baseline\nmodel. This is reasonable from an econometric perspective, as this model is mis-specified due to\nthe absence of controls for economic activity, the primary driver of emissions. To address this\nmisspecification, we include the natural logarithm of GDP as an additional control variable\n(column 3, Table ED15). Again, results remain consistent, with the coefficient for total policy\ndensity slightly larger in magnitude than in the baseline model.\nFor the interaction effect between policy density and absolute emission-reduction targets on\nabsolute levels of CO2 emissions, we add this in (column 4, Table ED15). The coefficient for the\ninteraction effect remains strongly significant, similar to in our baseline model with emission\nintensity as the dependent variable (main text, and Table ED4).\nAs additional sensitivity tests, we replace the natural logarithm of GDP with the natural\nlogarithm of population as alternative control variables in our models (columns 5 & 6, Table\nED15). Again, results remain remarkably consistent. The coefficients for policy density and the\nPolicies CO2 - Response to Reviewers 25\ninteraction effect with long-term targets are slightly larger in magnitude than the models with\nGDP as a control variable.\nOverall, we find that policy density is associated with more rapid emission reductions regardless\nof whether emission intensity or absolute emissions are specified as the dependent variable in our\nmodels. To avoid misspecification issues, we focus on the emission intensity models in main text,\nbut include the full set of absolute emission models in a new section of SI1 and Table ED15.\nMain changes in revised submission:\n- new absolute CO2 emission model results reported in Table ED15\n- new section of SI with discussion of absolute CO2 emission model results, with summary\nin main text\nEskander, S. M. S. U., & Fankhauser, S. (2020). Reduction in greenhouse gas emissions from national climate legislation.\nNature Climate Change, 10(8), 750-756. https://doi.org/10.1038/s41558-020-0831-z\nR3.3. This could contribute valuable insights into possible rebound effects of climate policies. If\npolicies incentivize efficiency improvements, possibly in connection with an economic stimulus,\npolicies could increase emissions despite relative decoupling of GDP from CO2 emissions.\nResponse:\nWe absolutely agree that the macroeconomic effects of climate policies on growth are critically\nimportant to understand, and central to discussions on decoupling, green growth, and degrowth.\nHowever, our econometric models are not able to isolate these recursive relationships in the\nCO2/GDP and climate policy time trends.\nAs noted in the previous response, our additional models with CO2 as the dependent variable are\nconsistent in showing the effectiveness of climate policies - the main aim of our study. So to the\nextent the reviewer’s observation of the potential rebound effects from efficiency-improving\nclimate policy holds, these effects are captured, but not isolatable, in the models. (We address\nendogeneity concerns that emission reductions may lead to climate policies in detail in R2.1).\nTo explore this further within out data, we reanalysed our policy dataset and found 13-15% of all\npolicies were explicitly linked with energy efficiency or energy savings. We reasoned that these\nwould be the main types of policy associated with possible rebound, but are a minority in our\npolicy stock variable.\nWe also note literature offering a more circumspect view of the magnitude of possible rebound\nfrom such efficiency policies, particularly Gillingham et al. (2013, 2016).\nSo although we cannot address the reviewer’s concern directly, overall we think our main\ninsights on climate policy effectiveness are robust.\nUsing CO2 emissions as the dependent variable emphasises absolute emissions trends that are\ninfluenced by not only country size and structural changes but also other time-varying factors\nsuch as energy demand and economic growth trajectories. While fixed effects mitigate some\nPolicies CO2 - Response to Reviewers 26\nconfounding influences, they cannot fully capture the dynamic interplay between absolute\nemissions, policy-induced efficiency gains, and economic output.\nGillingham, K., Kotchen, M. J., Rapson, D. S., & Wagner, G. (2013). Energy policy: The rebound effect is overplayed\n[10.1038/493475a]. Nature, 493(7433), 475-476. http://dx.doi.org/10.1038/493475a\nGillingham, K., Rapson, D., & Wagner, G. (2016). The Rebound Effect and Energy Efficiency Policy. Review of\nEnvironmental Economics and Policy, 10(1), 68-88. https://doi.org/10.1093/reep/rev017\nR3.5. While I think the fixed effects model specification generally is a good choice, the control\nvariables could be problematic in the sense of \"bad control\". For instance, one way to achieve a\nlower GDP CO2 intensity is to shift economic activity to the service sector while offshoring\npolluting manufacturing. This means climate policies could affect both the control (service value\nadded, imports, ...) and outcome variable (emissions). I would like to see a parsimonious\nspecification (with only the fixed effects and policy measures) as a baseline and a more detailed\ndiscussion of possible mechanisms.\nResponse:\nTo address the reviewers’ concern, we conducted additional sensitivity tests by removing the\ncontrol variable for the share of the services sector within a country. We then compared the\nmodified model with our baseline model. If the effect of shifting economic activity to the services\nsector while offshoring polluting manufacturing was associated with climate policy density,\nremoving the control should change results from the baseline model. However the coefficient for\npolicy density, as well as coefficients for the other controls, all remain virtually unchanged.\nAs an additional sensitivity test, we run a modified model that removes the control variable for\nthe share of imports in the country’s balance of payments. This should allow us to indirectly\naccount for carbon leakage that - as the reviewer notes - may occur when a higher share of\nimports with a larger carbon footprint replaces domestically produced goods. Again, the modified\nand baseline models are remarkably consistent, although in this case, the coefficient for total\npolicy density in the modified model reduces slightly in magnitude.\nWe show full model results in Table ED16. Overall, we do not find evidence contrary to our\ninitial findings. We reason that if significant carbon leakage effects were present, policy\naccumulation would lose relevance as an explanatory variable on emission intensity reductions\nwhich is not the case.\nMain changes in revised submission:\n- new parsimonious model sensitivity tests reported in Table ED16\n- new section of SI with discussion of model results\nR3.6. The authors state that there are no significant differences between instrument types\n(regulatory, economic, voluntary) but I was not able to find the corresponding results. It would be\nsurprising if voluntary instruments were as effective as mandatory types.\nResponse:\nPolicies CO2 - Response to Reviewers 27\nIn our original submission, we focused on the characteristics of national policy portfolios rather\nthan the relative contributions of specific instrument types. We did include results on portfolio\ndesigns that were specialised or concentrated on instrument types compared to those with a more\ndiverse mix of instrument types, finding the former to be more effective. However, as the\nreviewer notes, we did not report which instrument type was the most effective as our models\nwere not designed to evaluate this. (See R1.3 for a full discussion of this limitation of our\nmodelling approach).\nIn response to the reviewer’s concern, we have now run additional models for policy\ndensity by instrument type. Due to collinearity, we ran a separate model including controls for\neach of the 8 instrument types:\n regulatory: legal interventions, monitoring, and regulations\n economic: market-based and direct provision\n voluntary: planning, informational, and other voluntary\nFull results are shown in Table ED13. Given that our dependent variable is emissions intensity\n(CO2/GDP), we did not expect to find a clear effect given we were including as our independent\nvariable only a subset of all policies (coded as being of a particular instrument type). However,\nfive of the eight models show negative and significant coefficients for the policy density by\ninstrument type variable. The largest coefficient in absolute magnitude is for legal interventions\nand monitoring, both of which are categorised as ‘regulatory’. Three of eight models show\nnegative but non-significant coefficients. Two are for informational and other voluntary\ninstruments, both categorised as ‘voluntary’. The third is for the regulations (one of the\ninstrument types in the ‘regulatory’ category).\nThe null results for the voluntary instrument types is not surprising given the weaker incentives\nthese entail. This is also in line with the reviewer’s expectation in the comment.\nThe null result for regulations is surprising. We think this result has to do with increased\nheteroskedasticity (noise) within our coding of regulations as an instrument type which spans a\nwide range from binding performance and emission standards to weaker reporting, safety, or\ncompliance type regulations. For instance, such regulations include safety and performance\nrequirements for heaters, air conditioners or refrigerators in buildings (such as regulation “GB\n4706.13-2014 on the safety on household and similar electrical appliances” adopted in China in\n2016 or regulation “SI 994-1 on safety and performance requirements of air conditioners” adopted\nin Israel in 2009), mandatory reporting requirements for energy efficiency actions (such as a\nrespective regulation adopted in 2019 in the Netherlands) or guidelines for the estimation of\ngreenhouse gas emissions (such as a regulation adopted in 2017 in Australia which gives technical\nguidelines for GHG emissions estimation in energy facilities). Our country vignettes in SI2 further\nshow that the largest shares of regulations relate to the buildings and transport sector where\nemissions reductions have been relatively low, especially when comparing to emissions\nreductions in energy supply.\nAs also discussed in R1.4, we are also unable to control for the differing stringency of regulations\nwithin our policy sample.\nHowever, given the general limitation of these models trying to explain economy-wide emission\nintensity but with only a subset of all policies, we are reluctant to over-interpret this result.\nPolicies CO2 - Response to Reviewers 28\nMain changes in revised submission:\n- new model results in Table ED13\n- explanatory text in Methods and SI1 (linked from main text)\nR3.7. How common is the exit of policies in the data? When governments change so often does\ntheir ideological stance. For instance, Trump tried to undo environmental policies of the Obama\nadministration. Is this relevant for the results?\nResponse:\nReviewer 2 had very similar questions, so we have combined our response in full in R2.8 (see\nabove). In general our measure of policy density captures the comparatively rare occurrences of\npolicy dismantling indirectly because policy dismantling inversely correlates with new climate\npolicy adoption.\nPolicies CO2 - Response to Reviewers 29\nClimate policy portfolios that accelerate emission reductions\n2nd revised submission: Sep 2025\n(1st revised submission: Jan 2025, original submission Aug 2024)\nResponse to Reviewers.\nWe respond in detail to all the reviewers’ comments below with a summary of the main\nchanges in our second revised submission. Prompted by the reviewers’ recommendations\nand concerns, we have updated the manuscript, method and SI sections with new analyses,\nresults and argumentation particularly on (1) the relationship between policy density and\nstringency, (2) our use of control variables, (3) our use of attribution terminology, and (4) how\nour results compare with other recent publications on the effectiveness of climate policy. This\nrevised submission is further strengthened as a result, and we appreciate the reviewers for\nencouraging this.\ngreen text = editors’ and reviewers’ comments\nblack text = our response\nblue text (indented) = examples of new or revised text from manuscript\nREVIEWER COMMENTS\nReviewer #1 (Remarks to the Author):\nR1.1 The paper has improved a lot, and I think the paper presents interesting insights in\nthe impact of policies. I think the authors have addressed the many comments in a good way\nwith a very detailed response. Although for some comments they were not able to address\nthose, but this was due to good reasons as they indicated. I think one of my main omission\nof the analysis was policy stringency is missing, because the number of policies is not a\ngood measure of the quality and GHG impact of climate policies. The authors have included\nliterature that showed that policy stringency and policy density are also strongly correlated,\nso I think well addressed.\nR1.2 The work is original, but soon after their submission Stechemesser et al. published a\nsimilar analysis in Science. I asked for a comparison with Stechemesser et al., but I think\nthis is still not done yet. In their response to my reviewer’s comments they mentioned that\n“Stechemesser et al identify total emission reductions in the range 0.6-1.8 GtCO2 from their\nset of 69 policy-attributed structural breaks in emission trends. This is an order of magnitude\nsmaller than the estimate of 27.5 GtCO2 reductions in this study across all policy portfolios\nincluding continuously incremental reductions as well as major discontinuities.” I was\nsurprised to see this difference. However, the authors did not discuss the much lower\nreduction found by Stechemesser et al in their paper.\nR1.3 Action required: It would be good if the authors would discuss this major difference,\nand the possible reasons, as the reader may expect a comparison with Stechemesser et al.,\nas this study has a similar research objective. The comparison could also move to the SI,\nand only highlight the main conclusions in the main text.\nResponse:\nWe have included a new SI1 section with an extended literature review of attribution studies\nestimating emission reductions from climate policies, including the Stechemesser et al.\nstudy. This allows us to situate our attribution estimates in the literature, and discuss\ndifferences as a function of aim, methodology, and country and time samples. We also\n1\nsummarise this in main text as the reviewer suggested. The main text summary is\nreproduced here:\nBy comparing observed emission trends with a counterfactual no-policy scenario, we\nattribute 27.5 GtCO avoided emissions to the cumulative effect of all climate policy\n2\nportfolios over the period 2000-2022, of which 14.6 GtCO are in the BRIICS\n2\ncountries (see Figure Methods 1). In 2022, this is equivalent to 3.5 GtCO /yr which is\n2\nin line with other attribution estimates that use a variety of methods, country and time\nsamples (see SI1 for full discussion). Emission reductions attributed to climate\npolicies in the literature include: 2-7 GtCO /yr (global, to 2020) (Hoppe, Hinder et al.\n2\n2023), 1.3-5.9 GtCO /yr (133 countries, 1999-2016) (Eskander and Fankhauser\n2\n2020), 1.3 GtCO /yr (39 countries, 2005-2012) (Maamoun 2019), 1.3-2.5 GtCO /yr\n2 2\n(renewable energy policies only) (Hoppe, Hinder et al. 2023). Other studies attribute\nemission reductions of 28% to climate policies (48 countries, 2000-2021) (Nachtigall,\nLutz et al. 2024), of 0.8%-2.8% to each new climate law introduced (Eskander and\nFankhauser 2023), or of 4-15% to carbon pricing policies only (21 countries)\n(Döbbeling-Hildebrandt, Miersch et al. 2024).\nIn their recent study using difference-in-differences methods to make more robust\ncausal inferences than our fixed-effects model allows, Stechemesser, Koch et al.\n(2024) attributed total emission reductions of 0.6-1.8 GtCO to a set of 69 structural\n2\nbreaks in sectoral emission trends (41 countries, 2000-2020). Their country sample\nand study period are similar to ours, but their policy-attributed emission reductions\nare an order of magnitude lower. We interpret this as the result of their tighter focus\non statistically identifiable discontinuities in sectoral emissions caused by specific\ncombinations of sectoral policy instruments introduced or tightened in the preceding\n2 years. In contrast, our models assess policy portfolios’ cumulatively incremental\nimpact over the long-term; discontinuities are subsumed within these aggregate\neconomy-wide trends.\nThe new SI1 section includes further details on attribution methods and studies. For\nexample:\nIn Chapter 14 of the IPCC’s WG3 Sixth Assessment Report, Babiker, Bertoldi et al.\n(2022) define policy attribution as: “the extent to which emission-relevant outcomes\n(including the emission intensity of GDP) charted for countries as well as sectors and\ntechnologies may be reasonably attributed to policies implemented prior to the\nobserved changes.”\nMost ex-post policy impact assessments are for specific policy instruments in\nparticular contexts (Hoppe, Hinder et al. 2023). Very few studies assess collective or\n‘global’ impacts of policy stocks comprising multiple instrument types. Attribution\nmethodologies used to identify the effect of mitigation policies controlling for\nconfounding factors like socioeconomic conditions, fossil fuel prices, and trade-\nrelated policies, include “statistical attribution methodologies, including experimental\nand quasi-experimental design, instrumental variable approaches, and simple\ncorrelational methods” (Babiker, Bertoldi et al. 2022).\nWe align with the statistical attribution framework for ‘global’ policy impacts\nestablished by Eskander and Fankhauser (2020) in the climate policy attribution\nliterature, extending their testing of policy density (cumulative policy stocks) to\nadditionally assess the effect of policy stringency (see also Nachtigall, Lutz et al.\n2\n(2024)), policy instrument types, policy sectoral coverage, targets and policy-relevant\norganisations.\nIn their review of both ‘global’ and instrument-specific attribution literature, Hoppe,\nHinder et al. (2023) estimate a plausible range of emission reduction of 2-7\nGtCO e/yr compared to a no-policy counterfactual, equivalent to 4-5% of total GHG\n2\nemissions in 2020. Evidence from multiple studies span an attribution range of 1.3-\n5.9 GtCO /yr for different country samples and time periods:\n2\n Eskander and Fankhauser (2020) attribute reductions of 5.9 GtCO /yr (in 2016),\n2\nor 38 GtCO2-eq. cumulatively, to climate laws (1999-2016, 133 countries);\n Maamoun (2019) attribute reductions of 1.3 GtCO /yr (in 2012), equivalent to -\n2\n7%/yr, to climate policies pursuant to Kyoto Protocol emission-reduction targets\n(2005-2012, 39 countries with in UNFCCC Annex B);\n Babiker, Bertoldi et al. (2022) attribute reductions of 1.8-3 GtCO /yr to multiple\n2\npolicy instruments including energy-efficiency programmes and renewables\ndiffusion (unspecified time horizon & country sample);\n Grubb, Okereke et al. (2022) attribute reductions of 4-5 GtCO /yr (in 2019) to the\n2\ncumulative impact of policies (2010-2019, global);\n UNFCCC (2020) attribute projected reductions of ~3.8 GtCO /yr to the 38% of\n2\n>2500 implemented policies and measures for which estimates are available (36\ncountries in UNFCCC Annex 1);\n Hoppe, Hinder et al. (2023) draw on IRENA data to attribute emission reductions\nof 1.3-2.5 GtCO /yr to renewable energy policy.\npolicy instruments (carbon pricing) or targeted sectors (renewable energy), are:\n Stechemesser, Koch et al. (2024) attribute reductions of 0.6-1.8 GtCO from\n2\ndiscontinuous breaks in emission trends to 69 sets of policies in combination\n(2000-2020, 41 countries);\n Nachtigall, Lutz et al. (2024) attribute emission reductions of 28% to climate\npolicies compared to a no-policy counterfactual, emphasising the increasing\nstringency of policy portfolios over time (2000-2021, 48 countries);\n Eskander and Fankhauser (2023) attribute emission intensity reductions over the\nlong-term (>3 years) of 0.84–2.78% (territorial or production-based) or 0.91–\n2.61% (consumption-based) to each new climate law introduced (1996–2018, 111\ncountries);\n Döbbeling-Hildebrandt, Miersch et al. (2024) meta-analyse 80 ex post evaluation\nstudies of 21 carbon pricing schemes worldwide to generalise a de-biased effect\nof this specific policy instrument to the order of -4% to -15% emission reductions.\nR2.1 I would like to thank the authors for their efforts in revising and improving this study. I\nfeel that the study has substantially improved. I would like to highlight that the authors have\nconsiderably improved their discussions of endogeneity and attribution in the supplementary\npart of their paper. I think this discussion was necessary and has benefitted the overall\npaper. I appreciate the efforts by the authors to defend their attribution claims in the study\nand indeed I believe there is a good discussion (mainly the Granger causality testing)\nsurrounding the temporal setting that policies are antecedent to emission reductions.\nR2.2 However, I remain critical of the causal validity of the counterfactual construction and\nthe headline number of cumulative reductions of 27 GtCO2. I do not believe that simple\nprecedent from another study is enough to justify the term “attribution”. I remain partly\nconvinced that the policy density measure is more a representation of how liberal a society is\nand how important climate change is for society – but I’d be very careful to translate their\nresults into policy advice. Maximising policy density is clearly not what we should be doing –\nwe should carefully design a small number of (mixed) effective policies with clear aims and\neffect pathways rather than aim to simply increase policy density.\nResponse:\nWe appreciate the reviewer’s concern and we certainly want to avoid the main policy insight\nfrom our analysis to be about simple increasing policy stocks to maximise numbers density\nWe have revised the manuscript and SI in several way to address this concern.\nFirst, we have made more prominent our analysis of policy stringency as a correlate of policy\ndensity to emphasise that increasing stringency explains emission reductions rather than just\npolicy stocks per se. (This includes a new section in Methods on our policy stringency\nmodel). We also draw on the policy sequencing literature to explain why stringency and\ndensity tend to correlate as countries build on ‘easy wins’ to strengthen their climate action.\nNew or substantially revised text in our manuscript include:\n[in Results]:\nBuilding on prior attribution studies (see SI1), we find that both policy density\n(Eskander and Fankhauser 2020) and policy stringency (Nachtigall, Lutz et al. 2024)\nare associated with faster reductions in fossil CO2 emission intensity. We interpret\nthis result through the lens of policy sequencing (Linsenmeier, Mohommad et al.\n2022) which contends that policy portfolios become increasingly stringent as they\ndevelop (Pahle, Burtraw et al. 2018, Linsenmeier, Mohommad et al. 2022).\n(Stringency is the calibration of policy instruments, e.g., the specific level of a carbon\ntax, and is broadly equivalent to strictness (Schaffrin, Sewerin et al. 2015) or the\nextent to which climate policies incentivise or enable emission reductions (Creutzig,\nBecker et al. 2024)).\n…\n[in Discussion]:\nOur results confirm the basic insight from attribution studies that larger, more\ndeveloped (Eskander and Fankhauser 2020) or more stringent (Nachtigall, Lutz et al.\n2024) policy portfolios are associated with faster emission reductions. Policy stocks\ngrow due to complex policy design processes, interactions between policy goals and\nsectors, and competing political economic interests that all result in multiple policies\nor policy packages being introduced to tackle specific problems (Adam, Hurka et al.\n2019). Climate policy accumulation further results from the incremental sequencing\n4\nof policies over time to remove economic, societal, and political barriers to climate\naction (Pahle, Burtraw et al. 2018, Nascimento, den Elzen et al. 2023). Sequencing\nmeans policy density and policy stringency are strongly correlated as policies\nbecome more stringent as portfolios mature (Linsenmeier, Mohommad et al. 2022,\nNachtigall, Lutz et al. 2024). Stronger public demand for emission reductions further\ncontributes to policy portfolios developing towards greater stringency (Schaffer, Oehl\net al. 2021). This is why we interpret our main model result on policy density through\nthe lens of stringency, which also underpins our attribution claim (see SI1 for full\ndiscussion).\nSecond, we are now also clearer in our results and discussion that it is the design and\ncomposition of climate policy portfolios that explain emission reduction outcomes rather than\nsimply policy density. Indeed, we see this as the principal contribution of our study. This\nincludes more discussion on the importance of policy combinations or mixes as the reviewer\nnotes. New or substantially revised text in our Discussion section on policy mixes includes:\nOur results show that specialising on instrument types in policy portfolios is\nassociated with faster emission reductions. Different political traditions and contexts\nfavour different policy instruments (Meckling and Nahm 2018). In a comparative\nanalysis of renewable energy policy portfolios, Schmidt and Sewerin (2019) similarly\nfind that dominant instrument types vary by country, and that instrument\nspecialisation rather than diversity is associated with higher renewable energy\ndeployment.\nPolicy evaluation studies provide complementary insights on the effectiveness of\nspecific instruments (Peñasco, Anadón et al. 2021, Döbbeling-Hildebrandt, Miersch\net al. 2024). Over time, and with the increasing need for more stringent climate\naction, instrument choices have shifted from voluntary to regulatory and economic\n(Schmidt and Fleig 2018). In their attribution models, Nachtigall, Lutz et al. (2024)\nfind that in general market-based instruments and targets are associated with faster\nemission reductions than non-market (regulatory) instruments. Additional robustness\ntesting of our policy portfolio models using only subsets of policy instruments by type\nsimilarly show that portfolios weighted towards economic instrument types\noutperform others (see Methods and SI1).\nFrom a normative perspective, instruments like carbon pricing offer the most\neconomically efficient way of reducing emissions both within and across sectors\n(Sterner and Coria 2013, World Bank 2023). However, carbon prices have been\nrelatively low in many countries and carbon pricing has tended to be a more recent\ninstrument choice (Linsenmeier, Mohommad et al. 2022). The importance of\nregulatory and technology policies for emission reductions has been clearly\nevidenced in empirical assessments of low-carbon innovation (Grubb, Drummond et\nal. 2021) and in modelling analyses (Bertram, Luderer et al. 2015).\nConsequently, rather than single instrument dominance, policy mixes - including\nthose comprising different instrument types – tend to be more effective for multiple\nreasons: mutual reinforcement and positive spillovers; complementary time-varying\neffects; capacity for policymakers to address multiple problems simultaneously\n(Hoppe, Hinder et al. 2023). Stechemesser, Koch et al. (2024) demonstrate\nempirically that policy combinations are more effective for reducing emissions than\nstandalone policies, with carbon taxes an exception.\nThird, we position our attribution approach more clearly within the literature through a new\nsection in SI1 (reproduced in our response to R1.3) which also includes the difference-in-\n5\ndifferences (DiD) study by Stechemesser, Koch et al. (2024) whose design allows robust\ncausal inference of climate policy impacts on emissions. As the reviewer notes, our\nattribution methodology using two-way fixed-effect models does not directly establish\ncausality so we provide multiple other lines of evidence to back up our attribution claim. We\nalso further strengthen our model specification in an extended new SI1 section on controls\nand secondary confounding variables (reproduced in our responses to R3, particularly R3.3-\nR3.6). This includes further model testing designed to clean up the attribution of emission\nintensity reductions to climate policy portfolio elements.\nR2.3 At the very least, I would recommend to the authors to further review their language\nin lines 88, 100 and 295 and to directly compare their headline statements with\nStechemesser et al. in the main text, as they do in at the bottom of page 4 of the rebuttal to\nreviewer 1.\nResponse:\nWe’ve implemented all the reviewer’s suggestions on language and have also included the\ncomparison of our results with Stechemesser et al. in the main text. In all the instances of\nimplied causality the reviewer notes, we’ve either removed the claim completely, or changed\nthe language to emphasise association not causation. We then limit our attribution claim to\nthe conclusions, supported by literature (see R2.2). This text is as follows:\n[in Introduction]:\nAttribution studies use econometric methods to identify the general effect of climate\npolicies on emissions, controlling for other determinants of emission trends. These\nstudies have demonstrated the effect of larger policy stocks (Eskander,\nFankhauser et al. 2021, Eskander and Fankhauser 2023), of more stringent policies\n(Nachtigall, Lutz et al. 2024), and of specific policy combinations (Stechemesser,\nKoch et al. 2024). The difference-in-differences modelling used by (Stechemesser,\nKoch et al. 2024) allowed stronger causal attribution but was focused on a set of 69\ndiscontinuities in emission trends from recent policy introductions rather than the\ncumulative effect of policy portfolios over the long-term.\n[in Discussion]:\nBy comparing observed emission trends with a counterfactual no-policy scenario, we\nattribute 27.5 GtCO avoided emissions to the cumulative effect of all climate policy\n2\nportfolios over the period 2000-2022, of which 14.6 GtCO are in the BRIICS\n2\ncountries (see Figure Methods 1). In 2022, this is equivalent to 3.5 GtCO /yr which is\n2\nin line with other attribution estimates that use a variety of methods, country and time\nsamples (see SI1 for full discussion). Emission reductions attributed to climate\npolicies in the literature include: 2-7 GtCO /yr (global, to 2020) (Hoppe, Hinder et al.\n2\n2023), 1.3-5.9 GtCO /yr (133 countries, 1999-2016) (Eskander and Fankhauser\n2\n2020), 1.3 GtCO /yr (39 countries, 2005-2012) (Maamoun 2019), 1.3-2.5 GtCO /yr\n2 2\n(renewable energy policies only) (Hoppe, Hinder et al. 2023). Other studies attribute\nemission reductions of 28% to climate policies (48 countries, 2000-2021) (Nachtigall,\nLutz et al. 2024), of 0.8%-2.8% to each new climate law introduced (Eskander and\nFankhauser 2023), or of 4-15% to carbon pricing policies only (21 countries)\n(Döbbeling-Hildebrandt, Miersch et al. 2024).\nIn their recent study using difference-in-differences methods to make more robust\ncausal inferences than our fixed-effects model allows, Stechemesser, Koch et al.\n(2024) attributed total emission reductions of 0.6-1.8 GtCO to a set of 69 structural\n2\nbreaks in sectoral emission trends (41 countries, 2000-2020). Their country sample\nand study period are similar to ours, but their policy-attributed emission reductions\nare an order of magnitude lower. We interpret this as the result of their tighter focus\non statistically identifiable discontinuities in sectoral emissions caused by specific\ncombinations of sectoral policy instruments introduced or tightened in the preceding\n2 years. In contrast, our models assess policy portfolios’ cumulatively incremental\nimpact over the long-term; discontinuities are subsumed within these aggregate\neconomy-wide trends.\nR2.4 I would also suggest to clarify that their results do not challenge the validity of the\nTinbergen rule – but rather that their results indicate that policy-makers are not actually\nadhering to it. As currently framed, they seem to suggest that their results show that the\nTinbergen rule is not valid.\nResponse:\nWe’ve dropped all reference to the Tinbergen rule as our modelling is not designed to test it.\nWe’ve refocused the discussion of our policy density finding on its correlation with policy\nstringency as a better explanation of the emissions impact. We also discuss increasing\npolicy density in light of evidence on the effectiveness of policy combinations and policy\nmixes.\nR2.5 I would further remove the implicit reference to the EKC in line 144 – there remains\nsubstantial academic debate around the presence of an EKC in carbon emissions, so I\nwould rephrase that element.\nResponse:\nWe’ve dropped all reference to EKCs, recognising the ongoing debates around their\napplicability to GHG emissions.\nR2.6 I recommend to avoid using the abbreviation “IV” in Table 1 for independent variables\n– this in econometrics generally refers to an instrumental variable and could be confusing.\nResponse:\nWe’ve dropped shorthand notation to IVs (as well as DVs).\nR2.7 I would also ask the authors to show the full numbers in the two rightmost columns in\nTable Methods 2.\nResponse:\nWe’ve included the full model results from Eskander & Fankhauser in Table Methods 2.\nReviewer #3 (Remarks to the Author):\nR3.1. The authors have responded to my comments and mostly implemented appropriate\nchanges in the manuscript. I still have some major comments about the identification\nstrategy and interpretation of results.\nR3.2. The selection of control variables is not sufficiently justified and could substantially\nbias the coefficient of interest, yielding misleading results, even if well intentioned. In\n7\nresponse to my previous concern about bad control, the authors provided to additional\nmodels ED16 in which they separately exclude the service and import shares. In SI1 Section\n2.9, the authors state that the estimate of beta1 \"remains virtually unchanged\" when omitting\nthese variables. This is true for the service share but without the import share the point\nestimate of beta1 decreases by 35% and notably increases in variance. In my opinion, this is\na relevant change that suggests a mediating role of imports.\nR3.3. A rigorous engagement with the functional relationships of the included variables is still\nmissing, possibly in the form of a directed acyclic graph (Cinelli et al 2024). As parsimonious\nspecification in a two-way fixed effects setting, I would expect models with only the\nexplanatory variable of interest, especially since the FE already absorb a very large share of\nthe total variance in the outcome (~70% in this case).\nResponse:\nWe have strengthened our identification strategy including, as the reviewer suggests,\nthrough the use of directed acyclic graphs (DAG) to clarify the functional relationships\namong variables. We went back through relevant literature including Pearl (2009) and\nsubsequent work by Cinelli and others (Cunningham 2021, Celli 2022, Hünermund and\nBareinboim 2023, Cinelli, Forney et al. 2024) to inform our DAG that illustrates our research\ndesign and explicitly maps the assumed relationships among all variables included in our\nmodel specification. We first summarise the additional analysis we conducted on controls\nand model specification before explaining our DAG procedure in more detail.\nSummary of additional analysis on controls and model specification\nFrom an econometric perspective, the inclusion of GDP per capita, services share, and\nimport share aligns with standard practices in applied panel data analysis to block\nconfounding pathways. In a two-way fixed-effects framework, controlling for observed time-\nvarying confounders is necessary when the treatment is also time-varying and potentially\ncorrelated with omitted variables that affect the outcome (Angrist and Pischke 2010,\nWooldridge 2021). As emphasised by Cinelli and Hazlett (2019), even in high-dimensional\nsettings, control strategies grounded in causal assumptions help prevent omitted variable\nbias and enhance identification of causal effects. We use directed acyclic graphs (DAGs) to\nexplain and justify the role of our control variables (Cunningham 2021, Celli 2022, Cinelli,\nForney et al. 2024).\nOur sequential inclusion of controls mirrors the logic of a Frisch-Waugh-Lovell (FWL)\ndecomposition, whereby we partial out the effect of other covariates to isolate the variation in\npolicy density that is orthogonal to plausible confounders. The modest changes in the\ncoefficient magnitude and standard errors in later model stages (columns 6–9 of Table R1\nbelow) suggest that the control set reduces bias without introducing excessive\nmulticollinearity or instability. This pattern is consistent with an “unbiased conditional”\nspecification.\nDirected Acyclic Graphs (DAGs): Confounders & backdoor paths\nWe present the basic DAG in Figure R1a and then discuss the causal assumptions and roles\nof each variable.\nFigure R1. Directed acyclic graph (DAGs) of our research design: left panel [a] shows\nconfounders; right panel [b] shows secondary controls.\n[a] [b]\ntreatment (independent) variable capturing policy density; X represents GDP per capita; SER\nindicates the share of the services sector in the economy; and IMP denotes the share of imports;\nHF represents the Hodrick-Prescott filter; RoL denotes the Rule of Law index; and TEMP denotes\nthe temperature variation from the long-term mean.\nThe direct path from D to Y captures the causal effect of interest: the impact of policy density\n(D) on emission intensity (Y):\n(D) Policy Density → (Y) Emission Intensity\nTo obtain an unbiased estimate of the causal effect, it is necessary to block the following\nbackdoor paths using appropriate controls (pp79-85 in Pearl 2009, pp99-102 in Cunningham\n2021). These paths (Figure R1a) represent non-causal associations that could bias the\nestimation of the treatment effect:\n1. D  X  Y\n2. D  SER  X  Y\n3. D  SER  IMP  X  Y\n4. D  SER  IMP  Y\nBackdoor path 1:\n1. D  X  Y, in which X is GDP per capita (including its square term).\nThis backdoor path introduces spurious correlations between D and Y due to variation in the\nconfounder X that affects both D and Y. Here the confounder X is GDP per capita and its\nsquared term, a proxy for a country's development stage. Including the GDP squared term\ncaptures the non-linear (U-shaped) effect of development stage on emission intensity. In our\nstudy, climate policy density serves as a proxy for this transition so we expect a similar\nnonlinear relationship as for emission intensity. GDP per capita is a confounder as it\ncorrelates with the both the treatment and the outcome although in a non-causal way (see\nalso Table R2).\nBackdoor path 2:\n2. D  SER  X  Y, in which SER is the share of services in economic activity.\nControlling for GDP per capita closes one backdoor path, but introduces a second backdoor\npath from D to Y that arises due to variation in the share of economic activity in the services\nsector (SER) which is therefore a potential confounder. A higher services share is closely\nassociated with a country’s level of development. More developed economies tend to have\nlarger services sectors that yield greater value-added activity than manufacturing or\nagriculture (Herrendorf, Rogerson et al. 2014). In addition, specialisation in services such as\nreal estate, finance, and insurance prompts regulatory oversight that contributes to higher\n9\npolicy density. The delivery of services typically involves complex transactions and\ninstitutional arrangements, requiring more sophisticated regulatory environments to ensure\nefficiency, stability, and consumer protection (Rodrik 2000). This is also shown in Table R2.\nTo close this second backdoor path and avoid omitted variable bias, we control for the share\nof the services sector in the economy. Structural change within the services sector could\nalso directly reduce emission intensity, although to a lesser extent than the backdoor path\nshown in the DAG that we account for in our approach.\nBackdoor paths 3 and 4:\n3. D  SER  IMP  X  Y, in which IMP is the share of imports in a country’s\neconomy.\n4. D  SER  IMP  Y\nControlling for services introduces two additional backdoor paths that must be addressed to\navoid bias. First, specialisation in services can generate comparative trade advantages for\nthese types of exports, by extension increasing the share of imports of goods, specifically of\nmanufactured products. Policy density may then be jointly influenced by rising services-\nsector specialisation and increased goods imports as governments respond to trade\npractices (e.g. dumping) by introducing protective regulations to safeguard domestic\nindustries. As Rodrik (2018) argues, trade agreements become more about domestic rules\nand regulations than tariffs and non-tariff barriers.\nSecond, increased reliance on services-based economic activity and corresponding imports\nof manufactured goods is associated with reduced domestic emission intensity. This reflects\na form of carbon leakage through which more emission-intensive production is offshored to\ndeveloping countries (Eskander and Fankhauser 2023).\nControlling for imports closes two backdoor paths: between services and policy density, and\nbetween services and emission intensity.\nBad Controls & Colliders\nAccording to Cunningham (2021), it is common for a collider to entirely flip the sign of the\ncoefficient of interest when introduced in the model: “Angrist and Pischke (2009) talk about\nthis problem in a different way using language called “bad controls”. Bad controls are not\nmerely conditioning on outcomes. Rather, they are any situation in which the outcome had\nbeen a collider linking the treatment to the outcome of interest.”\nStarting with a model specification without fixed effects and including only our treatment\nvariable, we can see in column1-Table R1 that the coefficient for policy density is negative\nand significant as we expect. Controlling for country effects in column 2-Table R1, the\ncoefficient remains negative and significant. These first two models are called ‘biased\nunconditional’ in a relevant example used in Cunningham (2021, p110).\nOnce we introduce year fixed effects in column 3-Table R1 the coefficient flips its sign to\nbecome positive. This is not reasonable and the equivalent model in Cunningham (2021,\npp106-110) is called ‘biased biased’. Year dummies controlling for time fixed effects\neffectively function as a collider in our case. This is because when we control for time, we\nintroduce a backdoor path for policy density and emission intensity that is spurious and\ndistorts the nature of the causal relationship. Policy density tends to increase over similar\ntime periods for group of countries that are part of political unions and common economic\nmarkets. In the EU, for example: “More than half of the national measures are EU\nregulations. In some cases, the ratio is such that EU regulations account for 80 percent of\nnational climate change policies (Netherlands and Belgium)” (Jahn 2024). If policy density\n10\nincreases at similar rates in specific years for groups of countries within our sample, then\nsimple models of emission intensity reduction while controlling for yearly effects will\nunderstate the effect of policy density (e.g., the baseline parsimonious TWFE model in\ncolumn 3-Table R1).\nTo counteract this, we first need to introduce the confounder discussed above that accounts\nfor countries’ development stage (column 4-Table R1). This confounder captures better\nunderlying variation among countries within the same group and accounts for additional\nnuances in the effect over policy density conditional on countries’ economic status. We can\nobserve that the coefficient for policy density in column 4 becomes negative, as one would\nexpect, although it remains statistically non-significant. This model is still ‘biased biased’\nbecause we haven’t yet controlled for all backdoor paths opened due to the introduction of\nthe new confounder variable (see above). Introducing the additional two confounders that\naccount for share of services and share of imports, we cut off all backdoor paths and obtain\na negative and statistically significant coefficient for policy density. The model in column 6-\nTable R1 is the one that Cunningham (2021, p110) calls ‘unbiased conditional’.\nIn terms of standard errors variation, we can observe that there is minimal variation between\ncolumn 3 (0.000149) and column 6 (0.000154). When we introduce the final controls, we\nobserve a small correction in the magnitude of the coefficient, and minimal change in its\nstandard error variation (0.000163 in column 7 and 8, and 0.000169 in column 9).\nWe provide additional sensitivity analysis in table R2 that further supports our reasoning.\nOnce we drop time fixed effects, the coefficient for policy density always remains negative\nand statistically significant. This indicates that the change observed in Table R1 is due to the\ndiscussed collider effect, and by mainly shutting off backdoor pathways, we obtain ‘unbiased\nconditional’ estimates. Introducing controls one by one in the parsimonious model without\ntime fixed effects further confirms our expectations based on DAG formation presented in\nFigure R1 and confirms findings for model specification including time fixed effects. We can\nalso see that the coefficients for policy density are in general larger in terms of magnitude\nwhen excluding time fixed effects in Table R2 than the corresponding ones in Table R1.\nThe larger coefficients without time fixed effects represent overestimated effects that include\nspurious correlation from shared time trends. In other words, omitting time fixed effects\nwould fail to control for unobserved variation in emission intensities from 2000 to 2022,\nleading to biased model estimates.\nSecondary control variables - potential backdoor paths\nWe include a set of secondary controls in Figure R1b, which are not directly related to policy\ndensity, but may potentially have a spurious influence on the identified direct treatment effect\nif left uncontrolled. These variables are not part of the main DAG pathways shown in in\nFigure R1a. They help ensure robustness by capturing broader contextual variation not\nabsorbed by our main controls or fixed effects. More specifically, introducing GDP per capita\nmay raise concerns about opening alternative backdoor paths related to cyclical fluctuation\nin the business cycle and the nature of institutions. To capture the former, we introduce the\nHodrick-Prescott GDP filter that is commonly used to account for cyclical volatility in\neconomic activity. To capture institutional quality, we include the World Bank’s rule of law\nindex which varies across countries and time, reflecting path dependency in a country’s\ninstitutional development (Acemoglu and Robinson 2002). We expect both these secondary\ncontrols to be correlated with GDP per capita and emission intensity, and not to be\nsignificantly associated with policy density. Sensitivity analysis confirms this (see our\nresponse to R3.4 below).\nFinally, we introduce temperature variation from the long-term mean. This variable is\nexogenous to the treatment variable and helps capture non-linear temperature anomalies\n11\nthat could be associated with emission intensity fluctuations. It is not plausibly influenced by\npolicy density, and its inclusion strengthens the robustness of our estimates without\nintroducing endogeneity (see our response to R3.6 below).\nSummary of Revisions to Manuscript & SI:\nWe have extended and strengthened the explanation of controls in our Methods section, and\nhave included an edited version of this full response as a dedicated new section in SI1 on\nour selection and justification of controls and their effect on our identification strategy for the\neffect of policy density on emission intensity.\nWe distinguish the three confounders (GDP per capita, imports share, and services share)\nfrom the three secondary control variables (HP filter, rule of law, long-term temperature\nvariation), and link to corresponding new model results in relevant Extended Data Tables.\n(1) (2) (3) (4) (5) (6) (7) (8) (9)\nVARIABLES LOG(CO2/G LOG(CO2/G LOG(CO2/G LOG(CO2/G LOG(CO2/G LOG(CO2/G LOG(CO2/G LOG(CO2/G LOG(CO2/G\nDP) DP) DP) DP) DP) DP) DP) DP) DP)\nPolicy density) -0.00127*** -0.00450*** 0.000479*** -0.000177 -0.000247* -0.000454*** -0.000514*** -0.000505*** -0.000554***\n(0.000388) (0.000184) (0.000149) (0.000150) (0.000148) (0.000154) (0.000163) (0.000163) (0.000169)\nGDP per capita (log) 3.907*** 4.258*** 3.889*** 3.866*** 3.822*** 3.735***\n(0.251) (0.280) (0.252) (0.287) (0.285) (0.288)\nGDP per capita (log) -0.211*** -0.229*** -0.210*** -0.207*** -0.204*** -0.200***\ns quared\n(0.0131) (0.0147) (0.0134) (0.0151) (0.0150) (0.0153)\nServices share of GDP -0.00856*** -0.00948*** -0.00871*** -0.00896*** -0.00782***\n(0.00211) (0.00211) (0.00218) (0.00221) (0.00220)\nImports share of GDP -0.00435*** -0.00434*** -0.00435*** -0.00410***\n(0.000611) (0.000635) (0.000637) (0.000647)\nRule of law -0.0424 -0.0436 -0.0374\n(0.0298) (0.0298) (0.0301)\nHodrick-Prescott GDP -0.330 -0.354\nf ilter\n(0.254) (0.249)\nTemperature variation -0.0176**\n(0.00792)\nConstant -1.544*** -1.411*** -1.616*** -19.25*** -20.43*** -18.41*** -18.52*** -18.34*** -17.94***\n(0.0213) (0.00849) (0.00723) (1.199) (1.288) (1.143) (1.329) (1.323) (1.318)\nFE - Country NO YES YES YES YES YES YES YES YES\nFE - Year NO NO YES YES YES YES YES YES YES\nObservations 1,027 1,027 1,027 1,027 1,017 1,017 974 974 941\nR-squared 0.013 0.890 0.954 0.964 0.965 0.967 0.967 0.967 0.968\nNotes: Dependent variable is the log of emission intensity. Robust standard errors are reported in parentheses. *** p<0.01, ** p<0.05, * p<0.1\nED16(b) in Extended Data).\n(1) (2) (3) (4) (5) (6) (7) (8)\nVARIABLES LOG(CO2/GDP) LOG(CO2/GDP) LOG(CO2/GDP) LOG(CO2/GDP) LOG(CO2/GDP) LOG(CO2/GDP) LOG(CO2/GDP) LOG(CO2/GDP)\nPolicy density -0.00127*** -0.00450*** -0.00272*** -0.00237*** -0.00220*** -0.00221*** -0.00217*** -0.00196***\n(0.000388) (0.000184) (0.000165) (0.000155) (0.000141) (0.000155) (0.000154) (0.000153)\nGDP per capita\n(log) 6.324*** 6.710*** 5.580*** 5.690*** 5.727*** 5.267***\n(0.313) (0.314) (0.283) (0.303) (0.303) (0.299)\nGDP per capita\n(log) squared -0.347*** -0.364*** -0.303*** -0.309*** -0.312*** -0.287***\n(0.0160) (0.0158) (0.0148) (0.0157) (0.0158) (0.0156)\nServices share of\nGDP -0.0177*** -0.0175*** -0.0180*** -0.0163*** -0.0146***\n(0.00225) (0.00223) (0.00238) (0.00237) (0.00228)\nImports share of\nGDP -0.00662*** -0.00647*** -0.00669*** -0.00593***\n(0.000690) (0.000716) (0.000709) (0.000652)\nRule of law 0.0516* 0.0539* 0.0345\n(0.0296) (0.0296) (0.0297)\nHodrick-Prescott\nGDP filter 0.665*** 0.715***\n(0.206) (0.202)\nTemperature\nvariation -0.0503***\n(0.00763)\nConstant -1.544*** -1.411*** -29.42*** -30.55*** -25.22*** -25.75*** -25.90*** -23.88***\n(0.0213) (0.00849) (1.526) (1.520) (1.313) (1.413) (1.412) (1.387)\nFE - Country NO YES YES YES YES YES YES YES\nFE - Year NO NO NO NO NO NO NO NO\nObs. 1,027 1,027 1,027 1,017 1,017 974 974 941\nR-squared 0.013 0.890 0.944 0.949 0.955 0.955 0.956 0.960\nNotes: Dependent variable is the log of emission intensity. Robust standard errors are reported in parentheses. *** p<0.01, ** p<0.05, * p<0.1\naffected by the treatment and in turn can affect the outcome, namely GDP, the service share,\nand the import share. I would like to see these variables regressed on policy density,\nincluding also lagged density since adjustment to supply chains and sectoral composition\nlikely take several years. If policy density affects these variables, then they are bad controls,\nbias beta1, and should not be included (Angrist and Pischke 2009, Cinelli et al 2024).\nResponse:\nAs discussed above, we reason that GDP per capita, services share, and imports share are\nconfounders (not mediators as suggested by the reviewer). Their inclusion is necessary to\nreduce omitted variable bias and improve causal identification.\nIn response to the reviewer’s suggestion, we estimate simple regression models of these\nvariables on policy density (Table R3) and lagged policy density (Table R4). Consistent with\nthe relationships outlined in our DAG (Figure R1), we find that GDP per capita (and its\nsquared term), services share, and imports share are significantly associated with policy\ndensity. In contrast, the Hodrick-Prescott GDP filter and rule of law are not significantly\nassociated with policy density, confirming again our expectations (Figure R2). Instead, they\nare correlated with GDP per capita (Table R5) and emission intensity, supporting our\ndecision to treat them as secondary controls rather than confounders.\nTable R3. Sensitivity analysis: testing for associations between treatment variable (policy\ndensity) and control variables.\n(1) (2) (3) (4) (5)\nPolicy Policy Policy Policy Policy\nVARIABLES density density density density density\nGDP per capita (log) 498.5***\n(62.60)\nGDP per capita (log) squared -25.13***\n(3.108)\nServices share of GDP 2.288***\n(0.552)\nImports share of GDP -0.945***\n(0.142)\nHodrick-Prescott GDP filter 0.612\n(42.58)\nRule of law -6.795\n(6.513)\nConstant -2,412*** -99.32*** 82.09*** 41.17*** 49.74***\n(318.6) (33.64) (6.248) (0.645) (6.317)\nFE - Country YES YES YES YES YES\nFE - Year YES YES YES YES YES\nObservations 1,032 1,022 1,029 1,028 989\nR-squared 0.818 0.806 0.810 0.797 0.807\nThe dependent variable is policy density.\nRobust standard errors are reported in parentheses. *** p<0.01, ** p<0.05, * p<0.1.\nTable R4. Sensitivity analysis: testing for associations between lagged treatment variable\n(policy density) and control variables.\n(1) (2) (3) (4) (5)\nL1 Policy L1 Policy L1 Policy L1 Policy L1 Policy\nVARIABLES density density density density density\n(65.88)\nGDP per capita (log) squared -23.82***\n(3.241)\nServices share of GDP 2.113***\n(0.559)\nImports share of GDP -0.863***\n(0.140)\nHodrick-Prescott GDP filter -10.90\n(41.51)\nRule of law -1.688\n(7.009)\nConstant -2,326*** -91.10*** 76.43*** 38.85*** 42.58***\n(338.3) (34.13) (6.159) (0.626) (6.788)\nFE - Country YES YES YES YES YES\nFE - Year YES YES YES YES YES\nObservations 989 979 986 985 946\nR-squared 0.814 0.801 0.807 0.795 0.805\nThe dependent variable is one-year lagged policy density.\nRobust standard errors are reported in parentheses. *** p<0.01, ** p<0.05, * p<0.1.\nTable R5. Sensitivity analysis: testing for associations between GDP per capita and\nsecondary control variables.\n(1) (2)\nVARIABLES GDP per capita GDP per capita\nHodrick-Prescott GDP filter 1.606***\n(0.278)\nRule of law 0.345***\n(0.0340)\nConstant 10.51*** 10.18***\n(0.00364) (0.0334)\nFE - Country YES YES\nFE - Year YES YES\nObservations 1,028 989\nR-squared 0.969 0.974\nThe dependent variable is GDP per capita.\nRobust standard errors are reported in parentheses. *** p<0.01, ** p<0.05, * p<0.1\nSummary of Revisions to Manuscript & SI:\nAs noted in the previous response, we have extended and strengthened the explanation of\nconfounders and secondary controls in our Methods section, and as a dedicated new section\nin SI1 on our selection of model variables and their effect on our identification strategy.\nR3.5 There are some variables which are basically time-invariant and are already accounted\nfor by the unit FE, eg institutions. In that sense, the standard deviation reported in\nsupplementary table 1 is misleading because it does not reflect the variance that is actually\nused to estimate the models. It would be helpful to report also the within SD here, ie the SD\nof the FE residuals (Mummolo and Peterson 2018). I would assume that almost all variance\nin the variables related to institutions and economic structure is absorbed by the FE.\nFollowing Eskander and Fankhauser (2023), we reason that country-fixed effects include\ntime-invariant differences in socioeconomic context, political culture, institutional quality, and\nresource endowment between countries. With respect to institutional quality, we\nacknowledge that institutions are typically slow-moving and path-dependent, but over the\n2000–2022 period we have observed meaningful institutional shifts in several countries\nparticularly within the BRIICS including through crises, regime changes, democratisation,\nautocratization, and reforms (see Figure R4). These institutional shifts may impact the\neffectiveness with which climate policy density affects emission intensities (e.g., through\nchanges to policy credibility, monitoring, and enforcement). Considering this variation, we\ninclude the World Bank’s rule of law index as a control. The rule of law index from the\nWorldwide Governance Indicators (WGI) is reported annually and varies across countries\nand time (Versteeg and Ginsburg 2017).\nIn response to the reviewer’s concern, we computed and report both the overall standard\ndeviation and the within-unit standard deviation (i.e., fixed-effects-residualised) following\nMummolo and Peterson (2018). This allows us to examine the proportion of meaningful\nvariation that is actually used for identification in the fixed effects models. Table R6 follows\nthe structure of Table 1 in Mummolo and Peterson (2021) to show within-unit variation for\nrule of law. While reduced, it remains meaningful (retaining 17% of its total variance),\nsupporting our choice to include it in our models. Similarly, variables controlling for economic\nstructure (GDP per capita and its squared term, services share, and imports share) retain on\naverage 20% of their variation once we account for fixed effects. The treatment variable,\npolicy density, retains just under half of its variation, highlighting its suitability for our\nresearch design. As expected, secondary controls, Hodrick-Prescott filter and temperature\nvariation retain over two-thirds of their variance, consistent with their role in capturing cyclical\nand exogenous fluctuations.\nFigure R4. Variation in Rule of Law index 2000-2022 in BRIICS, with UK as comparison.\nTable R6. Standard deviation of independent variables before and after controlling for fixed\neffects (also included as Table ED19(a) in Extended Data).\n(1) (2) (3) (4)\nCoefficient SD Within unit SD Δ%\nGDP per capita (log) 3.735 0.64 0.12 -81.83\nGDP per capita (log) squared -0.200 13.12 2.25 -82.87\nServices share to GDP -0.00782 7.71 1.67 -78.31\nImports share to GDP -0.00410 25.86 5.36 -79.27\nRule of Law -0.0374 0.83 0.13 -83.80\nHodrick-Prescott GDP filter -0.352 0.019 0.013 -33.45\nTemperature variation -0.0176 0.52 0.40 -23.70\nColumn 1 shows the coefficients estimated in column 9 of Table R1. Column 2 indicates the standard\ndeviation of the independent variables for the full sample. Column 3 shows the within-unit standard\ndeviation meaning that variables are standardised for country and year fixed effects (Mummolo and\nPeterson 2018). Column 4 show the % difference (Δ) between standard deviations reported in\ncolumn 3 and 2.\nSummary of Revisions to Manuscript & SI:\nWe have included an edited version of this response (including Table R6) as a section in our\nSI1 discussion of controls and our model specification including both rule of law as a\nsecondary control variable and country fixed effects.\nR3.6 Temperature varies randomly, given the unit and time FE. Regressing temperature\nanomalies on policy density should yield an insignificant effect which might be a good\nplacebo test. As such it is no confounder / omitted variable and it is neither necessary to\ninclude it as control nor does including it bias the estimate of beta1.\nResponse:\nWe incorporate temperature anomalies from the long-term mean in our model to account for\nclimate variability, given that it might not be fully captured by year fixed effects, which\naccount only for linear time trends. Recent data from NASA (https://svs.gsfc.nasa.gov/5452)\nshow an increase in both the frequency and intensity of temperature anomalies over the last\ndecade, with the warming trend accelerating at different rates across countries.\nIn our view, regressing temperature variation on policy density does not constitute a robust\nplacebo treatment test in this context. This is because both policy density and temperature\nvariation are in linear form, while our baseline model estimates the treatment effect on a log-\ntransformed outcome. Consequently, we expect that this simple placebo test model would\nyield spurious results as it does not account for the accelerating relationship. In this, we\nfollow the caution advised by Hartman and Hidalgo (2018), who critique use of\nunderpowered placebo treatment tests for causal validation in applied political science.\nSimilarly, Eggers, Tuñón et al. (2024) emphasise the importance of matching the logic of the\nplacebo test to the research design.\nNonetheless, we agree that it is important to ensure the robustness of our research design,\nso we follow the reviewer’s suggestion to regress temperature variation on policy density\n(Table R7, column 1). As expected, results appear statistically significant, which we interpret\nas a model misspecification. To correct for accelerating trends and potential\nheteroskedasticity (particularly relevant given increasing temperature variability across\ncountries in recent years), we log-transform temperature variation. This log-linearised model\nconfirms that the coefficient for temperature variation is statistically non-significant, as\nexpected, thereby supporting the exogeneity of this control.\nTo further support our argument, we re-estimate the model using as dependent variable the\nlog of policy density and as independent variable (i) temperature variation (column 3), and\n(ii) the log of temperature variation (column 4). The absent of significant evidence in both\n18\nmodels confirms that once either or both variables are log-transformed, temperature\nvariation shows no systematic association with policy density.\nTable R7. Sensitivity analysis: testing for associations between treatment variable (policy\ndensity) and control variable for temperature variation from long-term mean.\n(1) (2) (3) (4)\nPolicy Policy LOG(Policy LOG(Policy\nVARIABLES density density density) density)\nTemperature variation -4.775*** -0.0285\n(1.469) (0.0206)\nTemperature variation (log) -0.783 0.00529\n(0.799) (0.0118)\nConstant 40.03*** 44.71*** 3.106*** 3.325***\n(0.686) (1.193) (0.0102) (0.0174)\nFE - Country YES YES YES YES\nFE - Year YES YES YES YES\nObservations 989 620 968 611\nR-squared 0.797 0.845 0.945 0.950\nThe dependent variable in columns 1 and 2 is policy density; in columns 3 and 4, it is the log of\npolicy density.\nRobust standard errors are reported in parentheses. *** p<0.01, ** p<0.05, * p<0.1.\nTo further test for robustness, we examine whether the inclusion of temperature variation\naffects identification of the treatment effect. Specifically, we compare the coefficient for policy\ndensity in the full model with temperature variation (Table R1, column 8) to the\ncorresponding coefficient in the reduced model without temperature variation (Table R1,\ncolumn 7,) using an F-test of coefficient equality. We estimate χ2 statistic equal to 0.70 with\np-value 0.40. This means that the test fails to reject the null hypothesis of no difference,\nsuggesting that including temperature variation in the model does not significantly alter the\nestimated treatment effect. This supports our decision to include it as a control without\ncompromising causal identification. Consequently, we retain the original temperature\nvariation variable in our baseline model specification. This is also consistent with the\nprecedents on which we build and so facilitates comparability of our model estimates with\nprior studies (Eskander and Fankhauser 2020, Eskander and Fankhauser 2023).\nSummary of Revisions to Manuscript & SI:\nWe have included an edited version of this response (including tables) in our SI1 discussion\nof controls and our model specification including temperature variation from long-term mean\nas a secondary control variable.\nR3.7 Since no track changes are provided, it is not immediately obvious what the authors\nchanged in the manuscript. However, I was not able to find any discussion of possible\nmediators in the main text (besides the moderating role of targets).\nResponse:\nOur revisions to the manuscript in the first round were extensive and we uploaded a track\nchanged version, so we are mystified this was not made available to the reviewer. We have\nchecked this with the journal production team, and trust our tracked change version of the\nmanuscript after this second round of revisions is accessible. As a back-up, we summarise\nhere our discussion of mediators which is substantially strengthened in this second revision\n(see R3.2 & R3.3 on model specification and DAGs).\nIn SI1, we include a new dedicated section on model specification that includes our\nconceptualisation of confounders in both basic and full DAGs, with further analysis of\nbackdoor paths and colliders. We reference this full discussion in Methods. As the reviewer\nnotes, we also have extended discussion in main text, Methods, and SI1 on long-term\ntargets and organisational dummies as moderators of climate policy portfolios’ effect on\nemission intensities.\nR3.8. Related to R3.5, in the current presentation of the results it is not clear how large the\neffect sizes are. Currently, the interpretation seems to be \"An increase in policy density by 1,\ndecreases emissions intensity by 0.05%\". Is this a practically relevant effect size? Is a\nmarginal change by 1 in policy density still plausible after partialing out the the FE? It would\nbe very helpful to report also estimates that are standardized using the within SD as\nsuggested by Mummolo and Peterson (2018). This way all variables would be on the same\nscale and the reader could easily assess the relevance of the effect sizes.\nResponse:\nOur treatment variable, policy density, is a count variable that captures the accumulation of\ndiscrete policies. Consequently we prefer to present effect sizes in terms of a one-unit\nchange, following (Mummolo and Peterson 2018): “Some might wish to convey treatment\neffects in the common scenario of a one-unit shift. This may be especially useful if the\ntreatment being studied is dichotomous or a count variable that takes only integer values, in\nwhich case unit shifts arguably make more substantive sense to consider.”\nThis is also consistent with prior studies that express effect sizes in relation to unit increases\nin policy density (Eskander and Fankhauser 2020, Nachtigall, Lutz et al. 2022, Eskander and\nFankhauser 2023).\nHowever, we agree that standardising coefficients using the within-group standard deviation\ncan improve interpretability, particularly when comparing effect sizes across variables\nmeasured on different scales. In response to the reviewer’s comment, and in line with the\ngrowing use of this method in applied political science, we implement the standardisation\nprocedure proposed by (Mummolo and Peterson 2018). We residualise each predictor with\nrespect to country and year fixed effects, calculate the within-unit standard deviation of the\nresiduals, and use these to standardise the independent variables before re-estimating the\nmodel.\nResults of this re-estimated model are presented in Table R8 below. We find that a 1\nstandard deviation increase in policy density (equivalent to 20 polices, see Table R6) is\nassociated with a 1% reduction in emission intensity. As shown in Table R8, the standardised\neffect of policy density is comparable in magnitude to that of key confounders (GDP per\ncapita, services share, imports share), and substantially larger than that of secondary\ncontrols (rule of law, Hodrick-Prescott filter, temperature variation).\nTable R8. Standardised coefficients using the within-group standard deviation (also included\nas Table ED19(b) in Extended Data).\n(1) (2)\nOriginal Coefficients - Standardised\nVARIABLES\nTable R1 column 9 Coefficients (within SD)\nTotal policy density -0.000554 -0.0112\nGDP per capita (log) 3.735 0.4369\nGDP per capita (log) squared -0.200 -0.4493\nServices share to GDP -0.00782 -0.0131\nRule of law -0.0374 -0.0050\nHodrick-Prescott GDP filter -0.352 -0.0046\nTemperature variation -0.0176 -0.0070\nColumn 1 shows the coefficients estimated in column 9 of Table R1. Column 2 shows the standardised\ncoefficients using the within-group standard deviation as proposed by Mummolo and Peterson (2018).\nSummary of Revisions to Manuscript & SI:\nWe have included additional text in the manuscript and Methods, Supporting Information,\nand Extended Data to capture this analysis. For example in Methods, we explain the\nmagnitude of effect size in relation to the confounders and secondary controls. In SI1, we\nprovide further explanation in a new dedicated section linking to full model results in Table\nED19.\nR3.9 In response to my previous comment, the authors provide interesting additional\nestimates by type of instrument in ED13. Here it is striking that the effect legal interventions\nis MUCH larger than any of the other types (eg 100 times larger than of market-based\neconomic instruments). Some other instruments do not significantly affect CO2 intensity at\nall. This seems like the effect could be driven entirely by legal instruments. is this the case,\nie is the coefficient still significant when omitting legal instruments from the policy density\nindex?\nResponse:\nTo directly address the reviewer’s concern, we perform the proposed test by removing legal\ninstruments from both the policy density index (Table R10-column 4). When comparing\nresults with the baseline model specifications (Table R10-column 2), we can see that the\ncoefficient changes only marginally from -0.116 to -0.117. This confirms that the main result\nis not driven by legal instruments.\nTo investigate further we went back to our policy coding to reexamine the descriptive\nstatistics for all the instruments in our dataset, but with a particular focus on legal and also\nmonitoring instrument types as these had much fewer occurrences (n<10) than the other\ninstrument types (all n>25). To improve robustness given these small sample sizes, we\nfolded legal and monitoring instruments together with regulatory instruments, reducing the\nnumber of instrument types from eight to six. We then re-estimate our original model (Table\nR10-column 2) using six policy instrument types (Table R10-column 3). Results remain\nvirtually the same with the coefficient for the instrument type HHI marginally changing from –\n0.116 to –0.114 and remaining strongly significant. This further confirms that this effect is not\ndriven by individual instrument types.\nTable R10. Sensitivity analysis with instrument type taxonomies\nBaseline Baseline New baseline Sensitivity\n(1) (2) (3) (4)\nVARIABLES Log(CO 2/GDP) LOG(CO 2/GDP) LOG(CO 2/GDP) LOG(CO 2/GDP)\nPolicy density -0.000554*** -0.000682*** -0.000688*** -0.000681***\n(0.000 169) (0.000165) (0.000 166) (0.000 165)\nHHI - 8 instrument -0.116***\ntypes\n(0.04 02)\nHHI - 6 instrument -0.114***\ntypes (legal &\nmonitoring combined\nwith regulatory)\n21\n(0.04 07)\nHHI - 7 instrument -0.117***\ntypes (legal removed)\n(0.0402)\nConstant -17.94*** -18.10*** -18.08*** -18.09***\n(1.318) (1.380) (1.378) (1.380)\nControls YES YES YES YES\nFE - Country YES YES YES YES\nFE - Year YES YES YES YES\nObservations 941 919 919 919\nR-squared 0.968 0.969 0.969 0.969\nRobust standard errors are reported in parentheses. *** p<0.01, ** p<0.05, * p<0.1.\nWe further replicate our original table ED13 with the single instrument type models using a\nthree category taxonomy: regulatory instruments, economic (including market-based and\ndirect provision instrument types), and soft (including planning, information, and voluntary\ninstrument types). This is also the more aggregated taxonomy we used in our main model\nfor testing instrument type diversity in policy portfolios.\nResults show a significant effect for economic instruments (–0.0015). The coefficient for\nregulatory instruments (–0.000359) is non-significant and similar in size to soft instruments (-\n0.00077) and one order of magnitude smaller than economic instruments. Table ED13 has\nthe full results including controls.\nGiven that our dependent variable is emission intensity (CO /GDP), we interpret these\n2\nresults with caution as the independent variable comprises only a subset of all policies\n(coded as being of a particular instrument type). Nevertheless, the null result for regulations\nis surprising.\nOur interpretation is that regulations as an instrument type span a wide range from binding\nperformance and emission standards to weaker reporting, safety, or compliance type\nregulations. Such regulations include, for example, safety and performance requirements for\nheaters, air conditioners or refrigerators in buildings (such as the regulation \"GB 4706.13-\n2014 on Safety on Household and Similar Electrical Appliances\" adopted in China in 2016),\nmandatory reporting requirements for energy efficiency measures (such as a regulation\nadopted in the Netherlands in 2019) or guidelines for estimating greenhouse gas emissions\n(such as a regulation adopted in Australia in 2017). This increases the heteroskedasticity\n(noise) within our coding of regulatory instrument types.\nStechemesser, Koch et al. (2024) also find that regulatory instruments tend to be more\neffective when combined with economic instruments: “some of the most widely used\nregulatory instruments and subsidy schemes may require complementary instruments to\nenable substantial emission reductions. The effect sizes of policy mixes that combine these\nnon–price-based instruments with taxation or reduced fossil fuel subsidies suggest that in\nmost cases pricing is the complement that enables effective emission reductions.”\n(Stechemesser, Koch et al. 2024).\nBest, Burke et al. (2020), Köppl and Schratzenstaller (2023), and Döbbeling-Hildebrandt,\nMiersch et al. (2024) provide further evidence supporting the effectiveness of market based\ninstruments, and in particular carbon taxation, in reducing CO emissions.\ninstrument type classification. We also replace our original 8 instrument type HHI diversity\nmeasure in all relevant models with the more robust 6 instrument type HHI that avoids single\ninstrument types with few occurrences in our dataset. This includes the main model reported\nin Table 1 of the manuscript and all relevant Extended Data Tables that report coefficients for\ninstrument type variables.\nIn SI1’s dedicated section on policy density by instrument type, we update the text to remove\ndiscussion of the previous 8 instrument type models, and focus on the results presented\nabove on the significance and effect of economic instruments relative to the other two\ninstrument type categories.\nIn Table ED13 we provide the full results for models that test policy density of only one\ninstrument type at a time.\nR3.10 It would be less confusing to present the regression results in Table 1 in a standard\nformat (models in columns, not rows). The caption should explain how to interpret the\ncoefficients (as in line 663ff). Also it could be clarified here what is included in the 3 types\nand 8 types.\nResponse:\nIn our original submission, we presented the regression results in standard format (models in\ncolumns, not rows), but another reviewer asked us to change the format as it created too\nmany blank cells. So in our revised submission, we presented the regression results in the\ncurrent format (models in rows) to address this problem but we agree it is harder to interpret.\nIn this second revision, we revert back to the standard format, but split the table into two, the\nfirst on the main effects of our policy portfolio variables (Table 1), the second reporting\ninteraction terms with our dummy variables (Table 2).\nWe have included a short explanation for interpreting coefficients in the table caption as the\nreviewer suggests. We’ve also included a note on the 6 instrument types for ease of\ninterpretation.\nR3.11 The link to the replication materials does not work for me so I cannot comment on the\navailability of the materials.\nResponse:\nWe had uploaded and checked the links for all our replication materials worked on our\nprevious submission, so as with the tracked changes version of our manuscript, we’re\nmystified why these did not work and apologise to the reviewer. In this submission we’ve\nagain uploaded our Stata .do and .dta files and checked accessibility. If these do not work for\nthe reviewer, we’d be grateful if the journal office could be alerted so we can try and work out\nwhat the problem is.\nAdditional Bibliography\nAcemoglu, D. and J. A. Robinson (2002). \"The Political Economy of the Kuznets Curve.\" Review of\nDevelopment Economics 6(2): 183-203.\nAdam, C., S. Hurka, C. Knill and Y. Steinebach (2019). Policy accumulation and the democratric\nresponsiveness trap. 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(2021) \"Two-Way Fixed Effects, the Two-Way Mundlak Regression, and Difference-\nin-Differences Estimators.\" Available at SSRN: https://ssrn.com/abstract=3906345 DOI:\nhttp://dx.doi.org/10.2139/ssrn.3906345.\nWorld Bank (2023). State and Trends of Carbon Pricing 2023. Washington, DC, World Bank.\n26"}, {"round": 3, "reviewer_comments": {"reviewer_1": "The new manuscript has successfully addressed the comments that I identified related to the comparison of Stechemesser et al, resulting in a much stronger and more robust paper.\nI want to thank the authors for detailed replies and the comprehensive additional work they have done to address both referees’ comments. The replies and additional sensitivity analysis have made clear that the main messages coming from the analysis are robust enough for this to be a meaningful contribution.", "reviewer_2": "I would like to thank the authors for their consideration of my comments and would like to congratulate them for their important and insightful addition to the literature.\nI have no more concerns and recommend acceptance.", "reviewer_3": "The authors have comprehensively addressed my comments and I have no further comments to give."}, "author_response": ""}]

Decision letter