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WorksEconomics, Econometrics and Finance

Measuring climate credibility? Talk, emissions, and corporate debt composition

Abstract

We examine whether a directional measure that compares emissions growth with earlier climate discussion is associated with corporate debt composition. The analysis links earnings-call climate language, LSEG/Refinitiv emissions, Capital IQ debt shares, RepRisk incidents, and accounting information for public firms over 2010–2021. The Emissions-to-Talk Index (ETI) is the central empirical measure, but we describe it literally rather than treating it as a general indicator of disclosure quality. In the baseline industry-and-year fixed-effect specification, a higher ETI is associated with a lower bank-debt share. The estimate falls by about four-fifths and is statistically insignificant when firm and year fixed effects are used on the same observations. It is also insignificant when the completed index is used to predict debt composition one calendar year later. Results based on the separate talk and emissions components, a ratio-free interaction, and complete talk–emissions categories lead to the same broad conclusion. Oster and Frank sensitivity calculations, alternative covariance estimates, exact year-sign bootstrap calculations, and leave-one-year-out estimates show that the contemporaneous result is sensitive to specification and inference. We also report exploratory comparisons by competition, financial health, opacity, and period; they do not show a consistent within-firm pattern. DealScan tests using unique facilities likewise show no common relation across facility incidence, spreads, maturity, security, and covenants. The evidence supports an association in the baseline industry-and-year specification, but not a causal claim that firms choose less bank debt to avoid monitoring or that lenders restrict credit because of the index.

JEL classification: G21; G32; Q54

Introduction

Corporate climate statements now form part of the information available to banks, bond investors, regulators and shareholders. Firms discuss transition plans, regulation, physical hazards and new business opportunities in earnings calls, while data providers assemble emissions records and environmental scores. These sources may affect financing, but they do not measure the same thing. Climate discussion may reflect a commitment, exposure to risk, an analyst’s question, or an explanation of current operations. Emissions can reflect abatement, output, acquisitions, divestitures and reporting choices. The relation between the two is therefore of interest, but its interpretation requires care.

To examine this issue, we use an Emissions-to-Talk Index (ETI). The index divides the firm’s year-on-year emissions growth by the frequency of climate language in executive sections of the previous year’s earnings calls. A high value indicates greater emissions growth per unit of earlier climate talk. It does not directly measure the truth of a statement, a missed target, or a manager’s intent. We ask whether firms with a higher ETI use a lower share of bank debt and consider monitoring avoidance as one possible explanation rather than the only explanation.

Our analysis asks whether this index is related to debt composition and whether the relation is stable across measurement and panel specifications. ETI is a directional ratio, not a symmetric distance between a stated target and its fulfillment. The underlying language measure counts climate-related bigrams but does not identify whether the passage contains a promise, whether the promise concerns emissions, or whether it was costly to make. A positive emissions change need not show that management failed to act, and a negative change need not show deliberate abatement. We therefore refer to ETI by its construction and use “greenwashing” only for externally recorded RepRisk incidents assigned to that category. This terminology is less ambitious, but it makes the empirical question more precise: is a firm’s emissions growth relative to its earlier climate discussion associated with its subsequent debt mix?

The question sits between two established literatures. Environmental performance, regulation, and climate exposure are related to loan and bond pricing [9, 15, 10, 25] and to corporate debt composition [17, 3, 28]. Work on debt choice shows that bank debt combines private information production, monitoring and renegotiation with possible bargaining and hold-up costs [12, 14, 13, 30, 21, 26]. These arguments do not yield a unique sign. A borrower that dislikes scrutiny may prefer less bank debt. A bank that views an observed discrepancy as risky may also supply less credit. Both channels lower the observed bank-debt share. By contrast, an opaque or exposed firm may value a bank’s information production and renegotiation capacity, which can raise its bank-debt share. An annual debt share is the outcome of borrower and lender decisions and does not identify which side moved.

That point matters for a monitoring-avoidance interpretation. Monitoring avoidance is a possible account of a negative coefficient, but it is not the only one. Nor does a lower bank-debt share necessarily mean that the amount of bank borrowing fell: a public bond issue can lower the share while bank debt is unchanged. Corporate green bonds became more prominent during the sample period [16]. The data do not identify those bonds or sustainability-linked loans, and they do not retain bank and bond component amounts. We can examine the bank, bond and residual debt shares, total debt, and accepted DealScan facilities, but we cannot separate borrower demand from lender supply or trace every change in the denominator.

Our data combine earnings-call climate measures, LSEG/Refinitiv Scope 1–3 emissions and environmental scores, Capital IQ debt shares, Compustat accounts, RepRisk incidents and Sautner climate-exposure fields. The firm-year panel contains 16,258 observations for 2,707 public firms from 2010 to 2021. Coverage varies by variable, so each table reports its own sample. The DealScan file contains 15,958 unique facilities. The principal loan tests use complete calendar years 2010–2019 because the extract ends in July 2020 and has no facilities in 2021.

We first estimate an industry-and-year fixed-effect regression and compare it with a firm-and-year fixed-effect model on the same observations. Firm effects absorb persistent disclosure style, production technology, financing policy and other time-invariant firm characteristics. We then distinguish a contemporaneous specification from a predictive one. The variable ETIitETI_{it} already combines emissions growth ending in year tt with talk in t−1t - 1. The contemporaneous model relates it to debt composition in tt. The predictive model instead relates ETIitETI_{it} to debt composition in t+1t + 1. Finally, we examine the separate talk and emissions components, their interaction and four complete talk–emissions categories. These checks retain observations with zero talk and do not divide by a small textual denominator.

We also undertake two sensitivity calculations for omitted variables. Oster’s proportional-selection statistic is reported for identical short and full samples under each fixed-effect design [29]. Frank’s impact threshold for a confounding variable is reported for the baseline industry coefficient, with an explicit qualification that Frank’s calculation is based on conventional least-squares inference [18, 6]. Because the baseline has only eleven year clusters, we compare homoskedastic, firm-only, year-only and two-way clustered standard errors, enumerate the one-way year-cluster wild-bootstrap sign assignments, and re-estimate the model after omitting each outcome year. None of these calculations removes endogeneity. They show how much the conclusion depends on the stated assumptions and covariance calculation.

The baseline result is sensitive to the fixed-effect structure. In the contemporaneous specification with industry and year effects, ETI has a coefficient of −0.0914-0.0914 (p=0.037p = 0.037). On the same observations used by the firm-effect estimator, the industry coefficient is −0.0961-0.0961 (p=0.016p = 0.016), whereas the firm-and-year coefficient is −0.0178-0.0178 (p=0.738p = 0.738). The fall of about 81.5 percent is thus not due to different observations or singleton removal. When the completed ETI is used to predict the next year’s bank-debt share, its coefficient is statistically insignificant with either fixed-effect structure. The separate components, continuous interaction and directional categories also yield no clear within-firm relation with bank, bond or other-debt shares.

Inference for the baseline coefficient is equally important. Its two-way clustered standard error is smaller than the homoskedastic, firm-clustered and year-clustered alternatives. The associated pp-values are 0.037, 0.169, 0.190 and 0.128, respectively. The one-way year-sign bootstrap gives p=0.250p = 0.250 when studentized with the year-cluster covariance. The industry-effect coefficient is negative in all eleven leave-one-year-out estimates, but is below the 5-percent threshold in only six; none of the corresponding firm-effect estimates is below the 10-percent threshold. These results do not overturn the industry-and-year estimate. They show that it is sensitive to the treatment of persistent firm differences and to inference with few time clusters.

The remaining results point in the same direction. The competition, financial-health, information-opacity and post-Paris patterns are visible mainly in industry-effect specifications. Most interactions are small and statistically insignificant with firm effects; the few raw exceptions are not persuasive after allowing for the number of related tests. RepRisk total and environmental incident counts have modest negative associations with bank share in some firm-effect models, but greenwashing-specific incidents do not. Those results concern external negative news and cannot be used as a second measure of ETI. DealScan regressions show no common pattern across facility appearance, amounts, spreads, maturity, security and covenants.

Our contribution is a detailed examination of a talk–emissions construction in a debt-choice setting. We compare industry-and-year estimates with same-sample firm-and-year estimates and show that the negative ETI association attenuates when persistent firm differences are absorbed. We also distinguish climate-language salience, operational emissions, topical exposure, vendor scores and external incidents instead of treating them as synonyms. This comparison complements studies that relate climate exposure, ESG ratings and adverse news to debt structure ([17, 3, 28]). It does not establish a new causal mechanism. The interpretation depends on the construction of the ratio, and a debt share alone cannot distinguish borrower from lender behavior.

The paper proceeds as follows. § 2 discusses the measurement and debt-choice arguments. § 3 describes the data and construction of ETI and the comparison measures. § 4 presents the empirical design and inference. § 5 reports the measurement evidence and central debt-composition results. § 6 presents the heterogeneity analyses. § 7 reports external incidents, alternative measures and DealScan tests. The final sections discuss interpretation, limitations and conclusions.

Climate information and debt choice

Words, environmental outcomes, and external events

We distinguish four measures that are observable in the data. The first is climate-language salience: how much of an earnings-call segment uses climate-related language. The Sautner dictionary was designed to measure participants’ attention to perceived firm-level climate exposure ([34]). It can capture discussion of an opportunity, physical exposure, or regulatory risk. This breadth suits exposure measurement but prevents a direct interpretation as favorable disclosure. Even prepared remarks are not necessarily voluntary claims about future emissions; they may address a risk that investors already regard as material.

The second object is an emissions outcome. Scope 1, Scope 2, and Scope 3 emissions refer to different operational boundaries and are subject to unequal coverage. Total emissions offer broader coverage but mix sources and may include estimates. Levels primarily reflect scale and production technology; intensity partly adjusts for scale; changes capture movement relative to a firm’s recent state. None maps one-for-one into managerial effort. For example, a divestiture can lower reported emissions without abatement, and a growing firm can increase total emissions while lowering intensity.

The third is a talk–emissions configuration. It joins two observables without claiming that either measures intent. One simple, directly observed configuration is high presentation talk accompanied by rising emissions. Its meaning is directional and easily stated. It can flag an observation for further investigation, but it is not a distance between a specific promise and its fulfillment. A continuous interaction has an equally limited interpretation: it asks whether the association of one standardized component depends on the other.

The fourth is an externally recorded controversy. RepRisk collects event-based negative news, including environmental incidents and a greenwashing category [32]. Such records originate outside the firm’s own call and are therefore recorded independently of it. They still depend on media coverage, the provider’s classification rules, and issuer matching, and should not be described as legal findings. Total ESG events also combine environmental, social, and governance content. An association for total incidents is not evidence of a climate-specific effect; an association for environmental incidents need not be greenwashing-specific.

These distinctions matter for the signaling argument. Cheap talk can be informative in equilibrium, but a costly-signaling interpretation requires the content of a commitment, a cost that differs by type, and conditions limiting imitation. The frequency variables do not identify those elements. Emissions abatement and verified green investment may be costly; uttering a climate bigram is not demonstrated to be costly. Accordingly, we do not formulate a directional hypothesis in which more climate talk automatically signals better environmental quality. We ask instead whether the segments predict subsequent emissions or external events after conditioning on prior state.

Our data distinguish presentation- and answer-section frequencies. If the underlying assignments are accurate, their information processes differ: prepared remarks are selected before the call, whereas answers respond to questions and may reflect contemporaneous information demand. The raw transcripts and parsing files are unavailable, so we cannot independently verify those assignments. A joint regression asks whether each segment measure contains incremental information conditional on the other. We treat any difference as an exploratory, descriptive segment-specific association, not evidence of motive, agency, or causality.

Competing implications for bank debt

Classic debt-choice theory offers no unconditional sign for the relation between climate information and bank debt. Banks economize on duplicated monitoring and produce private information [12, 14]. Private-debt placement and syndicated-loan structure respond to information asymmetry and monitoring needs [26, 35]. The value of that information can be greatest when public signals are incomplete. Private debt can also facilitate renegotiation when uncertainty is high. These forces imply that a firm with difficult-to-evaluate climate exposure may use more bank debt.

Informed lending has costs as well. A bank’s informational advantage can affect bargaining and create hold-up concerns [30, 21]. Managers may dislike investigation of statements that appear inconsistent with outcomes. If the perceived cost of scrutiny exceeds the information and renegotiation benefits, borrower demand for bank debt may fall. This is a monitoring-avoidance account. Its sign is conditional on an unobserved tradeoff and is not implied by delegated-monitoring theory alone.

Lender screening can generate the same observed sign for a different reason. If a bank interprets an external controversy or an apparent talk–emissions discrepancy as transition, governance, or reputation risk, it may restrict credit or change contract terms. Studies with lender identities and lender environmental commitments show what is required to examine this channel [10, 19, 23]. Borrower demand and lender supply jointly determine an accepted facility. Without rejected applications, lender attributes, or plausibly exogenous changes in lender policy, the two cannot be separated.

The loan data permit a limited check on these explanations. A screening account would ordinarily predict some combination of fewer recorded facilities, smaller reported amounts, higher spreads, shorter maturity, more security, or more covenants. A monitoring-value account could instead predict more bank borrowing and contract structures that facilitate oversight. A debt-share result unaccompanied by any loan-incidence or contract-term pattern provides only weak evidence about either explanation. Evidence based on accepted facilities remains selected, but considering several terms together is more informative than a bank share alone.

Debt composition also has an accounting dimension. Bank and bond shares are ratios to total debt, and firms hold other private or non-bank debt. The debt mix varies substantially within firms and across credit quality [11, 31]. An increase in bond issuance can reduce the bank share without reducing bank debt. Green bonds add an instrument that could matter for this substitution [16]. We therefore examine bank, bond, and residual other-debt shares together, and separately check total debt and debt-to-assets. We cannot identify green bonds or sustainability-linked loans in the available data, so we avoid attributing a share movement to those instruments.

These arguments guide the empirical tests without determining their outcome. Our main question is whether the ETI is associated with debt composition once persistent firm characteristics are absorbed and timing is made explicit. The analysis has three parts: whether such a relation is present in the panel estimates; whether it arises from the combined ratio or from its talk and emissions components; and whether the debt-share pattern is accompanied by loan-incidence or contract-term evidence. Finding a negative coefficient in the panel estimates would be consistent with both monitoring avoidance and lender screening. Finding no statistically detectable association would not show that banks disregard climate information; it would show only that this index has no detectable incremental relation with annual debt composition in the stated model.

Relation to climate finance and debt-choice evidence

The closest climate-finance studies examine several distinct margins. Chava [9] links environmental externalities to the cost of capital, while Fard et al. [15] studies environmental regulation and bank-loan costs. Degryse et al. [10] uses lender and borrower environmental characteristics to study loan contracting. Kim and Pouget [25] separates primary from secondary corporate bond markets and finds that the emissions relation differs across those settings. These papers make clear why an annual bank-debt share should not be described as “access” to public debt: it is neither an issuance decision nor a price.

Recent work is closer to the debt-mix outcome. Francis et al. [17] relates climate risk to debt structure, Asimakopoulos et al. [3] considers ESG ratings, and Newton et al. [28] examines external ESG reputation risk. Their explanatory variables do not have the same provenance or interpretation as ETI. Exposure can increase the value of relationship lending and contractual flexibility; negative news can affect perceived risk; an ESG rating can affect investors’ screening; and a talk–emissions ratio combines a firm’s words with an operational outcome. A finding for one is not a benchmark sign that every other measure should reproduce.

Research on greenwashing raises a separate construct issue. A text-based or machine-learning classification can be designed to identify misleading claims, as in Wang et al. [36]’s study of Chinese firms. Our call-frequency field was not trained for that task. It comes from the Sautner climate-exposure dictionary, whose purpose is to locate discussion of climate opportunities, physical exposure and regulation ([34]). We therefore compare ETI with RepRisk’s specifically coded greenwashing incidents but do not treat agreement as automatic. RepRisk records negative news and is itself affected by coverage and classification. We therefore use RepRisk as an external comparison, not as a definitive classification.

Our empirical contribution is to bring these distinctions to the debt-choice question. The baseline industry-and-year specification produces a negative association. The other tests ask whether that relation is present within firms, predicts a later debt mix, appears in ratio-free versions, or is accompanied by loan outcomes. This is a narrower contribution than claiming that ETI identifies greenwashing or monitoring avoidance. The available data support this narrower question.

Data and measurement

Firm-year and facility samples

Our master panel is indexed by Compustat gvkey and calendar year. It contains 16,258 unique firm-year observations for 2,707 firms from 2010 through 2021. Table 1 reports the sample flow, coverage, and descriptive statistics. Coverage differs across variables, so each regression table identifies its estimation sample, and either its notes or the sample-flow table reports the relevant firm and outcome-year cluster counts; we do not invoke a single “final sample.” The panel is unbalanced and contains 141 gaps. Exact-calendar changes and lags are missing when year t−1t-1 is not observed.

NNFirmsMeanSDMedianCoverage / window
Panel A: files and regression samples
Firm–year master panel16,2582,7072010–2021
Firm–years with bank, bond and other debt shares15,9122,6942010–2021
Full bank-share specification10,6912,0342011–2021
Same-sample firm/year specification10,4831,8262011–2021
Exact-lag ETI specification8,3341,5602012–2021
Unique-facility DealScan file15,9582,6312010–2020
Complete-year spread sample, contemporaneous index2,5075252010–2019
Complete-year spread sample, exact-lag index1,9884332010–2019
Panel B: firm–year variables
Bank debt share15,9120.3410.3620.2002010–2021
Public bond debt share15,9120.4980.3900.5532010–2021
Other debt share15,9120.1600.2810.0262010–2021
Emissions-to-Talk Index13,4100.00300.04390.00002010–2021
Presentation climate-term frequency ×10,000\times10{,}00016,04010.47427.1442.6072010–2021
Log Scope 1+2+3 emissions16,25812.7531.95212.6912010–2021
Annual change in log emissions13,4100.0240.2470.0002011–2021
Log assets16,0708.4481.8558.3992010–2021
Total debt/assets16,0220.2980.2340.2712010–2021
PP&E/assets15,3530.2620.2570.1632010–2021
Net income/assets16,0690.0160.1860.0342010–2021
Tobin’s Q15,8592.0631.5331.5382010–2021
Altman Z-score, winsorized13,2541.3081.8531.4422010–2021

Table 1. Table 1: Sample construction and principal variables. Notes: The master panel contains 16,258 firm–years. Debt shares are proportions and sum to one, subject to rounding. “ETI” denotes the directional ratio of the contemporaneous emissions change to prior climate-talk frequency. The unique-facility DealScan file contains 15,958 facilities. Exact calendar lags are set to missing across panel gaps. For the two complete-year spread rows, 2010–2019 is the analysis window; the fitted samples contain nine and eight outcome years, respectively.

The panel brings together precomputed earnings-call variables; LSEG/Refinitiv emissions, ESG, and Emissions-score fields; Capital IQ debt shares; Compustat accounting variables; RepRisk event counts; and Sautner climate-exposure variables. Our data begin with the annual call measures and vendor fields; they do not include the transcript-extraction files or the full sequence of initial merges. This matters for ETI, whose values can be used in the regressions but whose upstream text scaling, floor, and zero treatment cannot be regenerated exactly.

The DealScan file contains 15,958 unique facility identifiers for 2,631 firms from 2010 through 2020. We use one record per facility throughout. Of these facilities, 15,325 occur in the ten complete calendar years 2010–2019, of which 6,677 match the master panel on gvkey and year before regression-variable requirements. Across the full 2010–partial-2020 file, 6,866 facilities match. A failed match is not coded as an absence of borrowing. Facility coverage in 2020 stops on July 13, and no 2021 facilities are present; those years are excluded from loan-incidence and principal contract tests.

Earnings-call climate language

The earnings-call measures use climate-related bigrams based on Sautner et al. [34]. Let CC denote the climate dictionary and BictsB^{s}_{ict} the number of eligible bigrams in segment ss of call cc for firm ii in year tt. The conceptual segment frequency is

Talksicts=1Bicts∑b=1Bicts1{b∈C},s∈{P,A},(1)\mathit{Talks}^{s}_{ict} = \frac{1}{B^{s}_{ict}} \sum_{b=1}^{B^{s}_{ict}} 1\{b \in C\}, \qquad s \in\{P,A\}, \tag*{(1)}

where PP denotes the management presentation and AA management answers. The data contain annual, precomputed segment frequencies. Because they do not include the upstream transcripts and aggregation program, we describe the available fields rather than claiming to re-create speaker parsing or call-to-year weighting.

Presentation and answer frequencies are nonnegative, right-skewed, and have many observed zeros. The exploratory segment analysis therefore applies the transformation

Talk~its=z[log⁡{1+10,000Talkits}],(2)\widetilde{Talk}_{it}^{s} = z[\log\{1 + 10{,}000 Talk_{it}^{s}\}], \tag*{(2)}

where z[⋅]z[\cdot] standardizes over the observed firm-year sample. The logarithm is defined at zero and preserves ordering; standardization then centers and scales the transformed measure. Both segments enter the segment-comparison regression jointly. For the debt analysis, we standardize presentation talk within two-digit SIC industry-year cells, so the variable compares a firm’s climate salience with contemporaneous firms in the same broad industry. Cells with fewer than three observations are excluded from standardization.

We call these fields climate-language salience. The presentation field is more firm-directed than the answer field, but it still may describe adverse exposure rather than environmental commitment. The Sautner overall, opportunity, regulatory, and physical exposure measures are comparison variables. A strong correlation with them is expected because the measures share a dictionary and transcript source; it shows common climate-language content, not independent evidence of green quality.

Emissions and climate-information constructions

Let EitE_{it} denote the available LSEG/Refinitiv total Scope 1–3 field. We examine log⁡Eit\log E_{it}, the exact-calendar change

Δlog⁡Eit=log⁡Eit−log⁡Ei,t−1,(3)\Delta\log E_{it} = \log E_{it} - \log E_{i,t-1}, \tag*{(3)}

and log emissions intensity, defined using revenue. Total emissions provide much broader coverage than the scope-specific fields. The data do not identify, observation by observation, whether the total is reported, estimated, or carried forward, and they do not preserve historical data vintages. Total emissions are exactly unchanged from the preceding year in 3,929 firm-years. We keep these observations but do not assume that equality means no change in underlying operations.

We define the Emissions-to-Talk Index (ETI) as percentage emissions growth divided by lagged presentation-plus-management-answer talk:

ETIit=(Eit−Ei,t−1)/Ei,t−1Talki,t−1PA.(4)ETI_{it} = \frac{(E_{it} - E_{i,t-1})/E_{i,t-1}}{Talk_{i,t-1}^{PA}}. \tag*{(4)}

We use the ETI in the baseline regressions and assess its timing and distributional sensitivity, winsorizing it at the 1st and 99th percentiles in the distributional checks.

The data contain two additional ratios used only for comparison: emissions growth divided by lagged presentation talk and the change in log emissions divided by the change in presentation talk. Appendix Table A1 summarizes these ratios. We also form exact-calendar versions from their components, setting a zero denominator to missing, and compare them before and after fixed 1st/99th-percentile winsorization in Appendix Table A6. These ratios are not central to the interpretation because a small denominator can assign enormous leverage to an observation for reasons unrelated to the economic discrepancy of interest.

The principal ratio-free checks avoid division. Within two-digit SIC industry-year cells, let

Tit=zst(TalkitP),Dit=zst(Δlog⁡Eit),Iit=z(TitDit),(5)T_{it} = z_{st}(Talk^{P}_{it}), \qquad D_{it} = z_{st}(\Delta\log E_{it}), \qquad I_{it} = z(T_{it}D_{it}), \tag*{(5)}

where the outer z(⋅)z(\cdot) restandardizes the product over the panel. The continuous model enters TitT_{it}, DitD_{it}, and IitI_{it} jointly. The main ratio-free and common-sample models scale continuous information measures to a one-standard-deviation change and use information dated t−1t - 1. ETI, the comparison ratios, the moderator models, and the DealScan specifications retain the units and timing stated in their table notes. We also form four complete quadrants according to whether presentation talk is above versus at or below its industry-year median and whether emissions rise. Low talk with non-rising emissions is the reference category; the other indicators are high talk/non-rising emissions, low talk/rising emissions, and high talk/rising emissions. The last category is a simple, observable configuration, not a classification of managerial intent.

The main ratio-free, segment, and complete-year DealScan analyses use information from firm-year tt to predict an outcome in t+1t + 1. Equivalently, those regressions place an exact one-year calendar lag on the right-hand side. The ETI and the ratio comparisons retain their contemporaneous timing and are labeled accordingly. This matters for ETI because the index already uses emissions growth ending in its stated year and talk from the preceding year. Using the index contemporaneously with debt is not the same as asking whether the completed index predicts later debt structure.

Debt, controversy, score, and loan outcomes

Capital IQ supplies bank debt and public bond debt as shares of total debt. We define other-debt share as one minus the two reported shares. The three shares sum to one up to storage precision. Examining them jointly helps identify whether an estimate is bank-specific, but the data do not contain the component dollar amounts needed to decompose a change in ratios. We use Compustat long- and short-term debt to construct total debt and debt-to-assets only to check the role of the denominator; we do not infer bank or bond amounts by multiplying shares by Compustat debt.

RepRisk fields count externally recorded negative-news incidents [32]. The main criteria are an indicator for at least one greenwashing incident, log⁡(1+n)\log(1 + n) greenwashing incidents, log⁡(1+n)\log(1 + n) environmental incidents, and log⁡(1+n)\log(1 + n) total ESG incidents. Continuous incident counts are standardized when used as financing predictors. In comparisons with later external outcomes, those outcomes are dated one year after talk, and the specifications include their exact calendar lags. For financing, controversies are dated one year before the debt or loan outcome.

The simultaneous information comparison also includes standardized Sautner opportunity, regulatory, and physical exposure, and standardized LSEG ESG and Emissions scores. These measures are deliberately not pooled into a composite. Their source and content differ: the topical variables are call-based exposure, the LSEG fields are vendor scores, and RepRisk counts external negative news. The joint regression asks whether any measure adds information about debt composition after conditioning on all the others.

At the firm-year level, DealScan outcomes are an indicator for at least one matched facility, log⁡(1+facility count)\log(1 + \text{facility count}), log⁡(1+reported facility amount)\log(1 + \text{reported facility amount}), average all-in-drawn spread, and average maturity. “No matched facility” means no facility observed in the DealScan extract for that firm-year; it does not mean an application was rejected. At the facility level, outcomes are log⁡all-in-drawn spread\log\text{all-in-drawn spread}, log⁡maturity\log\text{maturity}, an explicitly reported secured indicator, the number of financial covenants, and revolver status. The source units of reported facility amount are not treated as verified U.S. dollars in the all-currency sample. We report a U.S.-dollar-only sensitivity analysis separately. In the principal loan analyses, unknown security status, which occurs for 5,518 facilities in the facility file, remains missing rather than being coded unsecured.

Controls

Firm-year controls are log⁡\log assets, total debt divided by assets, net property, plant and equipment divided by assets, net income divided by assets, Tobin’s QQ, and the winsorized Altman ZZ-score [2]. Financing and controversy models also include the prior emissions state as appropriate. The emissions tests in Table 2 build the control set from Compustat components. Other predictive models use exact-calendar lags and build debt-to-assets as (dltt+dlc)/at(dltt + dlc)/at and the other accounting ratios from Compustat components. Some specifications use the precomputed control fields. Their leverage definition differs from debt/assets, and several fields align with later inputs. The predictive specifications instead use controls reconstructed at exact calendar lags.

Talk measure or horizonIndustry + year effectsFirm + year effects
EstimateNNFirmsEstimateNNFirms
Panel A: log emissions at t; talk measured at t − 1
Presentation and management-answer portions2.7525 (1.0068) p=.021p = .02110,6822,114−0.1160 (0.2859) p=.693p = .69310,4541,886
Prepared-presentation portion37.8280 (13.6385) p=.020p = .02010,6712,1141.2744 (4.2558) p=.771p = .77110,4431,886
Panel B: cumulative change in log emissions from t to t + h; presentation talk measured at t
h=1h = 10.00235 (0.00247) p=.364p = .36410,6732,0200.00355 (0.00389) p=.382p = .38210,4771,824
h=2h = 20.00193 (0.00322) p=.563p = .5638,6341,8250.00233 (0.00514) p=.661p = .6618,3711,562
h=3h = 30.00052 (0.00438) p=.908p = .9086,8031,5650.00015 (0.00600) p=.981p = .9816,5631,325
Panel C: log emissions intensity at t; presentation talk measured at t − 1
Log emissions intensity0.00368 (0.00231) p=.142p = .14210,4241,809−0.00156 (0.00492) p=.757p = .75710,4241,809

Table 2. Climate talk and subsequent emissions. Notes: Each estimate is followed by its two-way firm/year-clustered standard error and unadjusted two-sided pp-value. Panel A relates current log emissions to prior-year talk and uses rebuilt controls. TalkFreq for the combined presentation and management-answer portions is scaled by ten, while presentation-only talk is a raw fraction, so their coefficients should not be compared in magnitude. Panels B and C standardize presentation talk within two-digit-industry/year cells and control for the prior outcome, assets, debt/assets, PP&E/assets, profitability, Tobin’s Q and Altman Z-score. Panel B outcomes require an exact hh-year calendar match. Panel A has 11 year clusters. Panel B has 11, 10 and 9 year clusters for h=1,2,3h = 1, 2, 3, respectively; Panel C has 11. Both firm/year covariances in Panel A and the industry/year covariance for Panel B at h=1h = 1 required a positive-semidefinite repair; no other displayed covariance did. The firm-effect estimates do not indicate that greater presentation talk precedes lower emissions or emissions intensity over these horizons.

Facility regressions add the relevant contract controls. Spread models include log⁡\log reported facility amount, log⁡\log maturity, and security status; maturity models include amount and security; security models include amount and maturity; and covenant and revolver models include amount, maturity, and security. We also add pooled loan-type, deal-purpose, and currency categories. Source categories represented by fewer than 20 facilities are pooled to avoid cells that cannot support the fixed-effect comparison.

Empirical design

Segment-level comparisons with external outcomes

We first examine whether prepared and answer-segment talk contain different information about subsequent outcomes. For outcome VitV_{it}, the primary specification is

Vit=βPTalk~i,t−1P+βATalk~i,t−1A+ρVi,t−1+θ′Xi,t−1+μi+τt+εit.(6)V_{it} = \beta_{P}\widetilde{Talk}^{P}_{i,t-1} + \beta_{A}\widetilde{Talk}^{A}_{i,t-1} + \rho V_{i,t-1} + \theta^{\prime}X_{i,t-1} + \mu_i + \tau_t + \varepsilon_{it}. \tag*{(6)}

The outcomes are emissions change, LSEG scores, greenwashing incidence and count, environmental incidents, and incidents classified as misleading communication. The lagged dependent variable is included in the persistence specification reported in the main table; for emissions change it reduces the sample because two consecutive calendar changes are required. The short panel means this dynamic fixed-effect model should be read only as a predictive exercise, not as a structural dynamic model. We also estimate the equation without Vi,t−1V_{i,t-1} and use industry effects in place of firm effects on the identical sample.

Debt-composition models

For debt outcome YitY_{it}, the central model is

Yit=α+βETIi,t−h+ϕlog⁡Ei,t−1+θ′Xi,t−1+μi+τt+uit.(7)Y_{it} = \alpha+ \beta ETI_{i,t-h} + \phi\log E_{i,t-1} + \theta^{\prime}X_{i,t-1} + \mu_i + \tau_t + u_{it}. \tag*{(7)}

We use two values of hh. With h=0h = 0, the emissions change embedded in ETIitETI_{it} and debt share YitY_{it} refer to the same year, while the talk denominator refers to t−1t - 1. With h=1h = 1, the completed index at t−1t - 1 is related to debt share at tt. The latter is the predictive specification. We report both because they answer different timing questions.

We estimate (7) for bank, bond, and other-debt shares. Firm effects absorb time-invariant business models, average disclosure styles, production technologies, industry affiliation, and persistent debt policies. Year effects absorb common shocks. Under h=1h = 1, β\beta is the conditional association between a change in a firm’s completed ETI and its debt share one year later. Under h=0h = 0, it is a contemporaneous conditional association and does not establish temporal ordering.

The same-sample comparison replaces μi\mu_i with two-digit SIC fixed effects and retains year effects. Its sample is exactly the sample used by the firm-effect model after recursive singleton removal, so differences between the two coefficients cannot be attributed to missing observations. The industry model combines between- and within-firm variation; it is not a second primary result.

The ratio-free models are measurement checks on the same question. For climate-information vector Gi,t−1G_{i,t-1}, we estimate

Yit=α+β′Gi,t−1+θ′Xi,t−1+μi+τt+uit.(8)Y_{it} = \alpha+ \beta^{\prime}G_{i,t-1} + \theta^{\prime}X_{i,t-1} + \mu_i + \tau_t + u_{it}. \tag*{(8)}

In the continuous specification, GG contains presentation talk, emissions change and their interaction. In the categorical specification, it contains the high-talk/non-rising, low-talk/rising and high-talk/rising cells, with low talk/non-rising emissions omitted. These models ask whether the conclusion depends on division by talk. They are not alternative definitions of ETI chosen to produce a particular sign.

Debt shares are observed proportions, not censored realizations of a latent variable, so we use linear fixed-effect models. Binary outcomes use linear-probability models as descriptive checks, and counts use log⁡(1+n)\log(1 + n). We emphasize direction, stability, and family-wise inference for these bounded and sparse outcomes.

The full comparison expands GG to include presentation talk, emissions change, their interaction, RepRisk environmental incidents, a RepRisk greenwashing indicator, the three Sautner topical exposures, and the two LSEG scores. All ten information variables enter simultaneously. Continuous measures are standardized. We ask whether any source has an additional association with debt composition after conditioning on the others in a common sample.

Controversy, total-debt, and DealScan tests

The controversy analysis applies Equation (7) first to standardized environmental incidents and the greenwashing indicator, then to total incidents alone, and finally to environmental and total incidents together. The conditional model asks whether the relation is specific to environmental incidents. If the environmental coefficient loses magnitude and statistical significance after total incidents are included, it does not provide distinct evidence of an environmental association. We also estimate a distributed model with leads and lags and descriptive event-time coefficients around the first observed positive environmental count. The event-time model is explicitly descriptive. Incident recording is not a staggered treatment, firms can have repeated events, and the pre-event coefficients do not support a causal design.

Total-debt checks replace the share outcome with log total debt or total debt-to-assets and add the lagged dependent variable. They ask whether a share association is accompanied by a change in overall borrowing. They cannot recover bank-debt or bond-debt amounts.

The DealScan models retain the timing and fixed-effect structure of Equation (7). Firm-year models examine appearance and volume in the DealScan extract. Facility models condition on the observed contract and therefore estimate associations among accepted facilities. The complete-year analysis clusters by firm and outcome year. The supplementary contemporaneous ETI models for non-price facility terms in Table A16 include partial 2020 and use firm clusters only. Because multiple facilities may belong to the same firm-year, the firm cluster accounts for repeated borrower observations, while the year cluster in the complete-year analysis accounts for common credit conditions.

OutcomeIndustry + year FEFirm + year FENIYN_{IY}NFYN_{FY}RIY2R^{2}_{IY}RFY2R^{2}_{FY}
Number of financial covenants−0.034-0.034<br>(0.019)(0.019)<br>p=.085p = .0850.0180.018<br>(0.019)(0.019)<br>p=.334p = .3345,0444,8470.1550.662
Secured indicator0.0050.005<br>(0.010)(0.010)<br>p=.595p = .595−0.014-0.014<br>(0.010)(0.010)<br>p=.138p = .1385,0444,8470.2550.727
Log maturity0.0090.009<br>(0.008)(0.008)<br>p=.225p = .2250.0070.007<br>(0.012)(0.012)<br>p=.544p = .5444,9934,7960.1690.363

Table A16. Non-price terms of accepted facilities and the Emissions-to-Talk Index

Inference and multiplicity

Principal firm-year standard errors are clustered two ways, by firm and year [8]. Reported pp-values and confidence intervals use a tt reference distribution with degrees of freedom based on the smaller cluster dimension. Depending on the sample, there are only eight to eleven year clusters. We therefore report the cluster counts prominently and treat conventional threshold crossings as suggestive unless they are stable across these checks.

We also use alternative covariance estimators, leave-one-year-out ranges, and an exhaustively enumerated, null-imposed one-way year-cluster wild-bootstrap-tt for six coefficients selected in advance [7, 33]. The last calculation removes Monte Carlo error but omits within-firm dependence and therefore does not replace the primary estimator.

Holm pp-values control family-wise error within each declared specification family [20]; the relevant table notes list the terms or outcomes included in that family. Broader section-wide and global adjustments are reported where relevant. Raw values show where small pp-values arise, while the adjusted values guard against placing weight on isolated results from a large set of related outcomes. We apply the stated timing, fixed-effect, and multiplicity checks across each declared family and do not interpret isolated raw threshold crossings as primary evidence.

If the multiway covariance is indefinite, we use the eigenvalue correction described by Cameron et al. [8]: negative eigenvalues are set to zero and the model is flagged. This issue is concentrated in expanded DealScan category grids; the primary ratio-free and separate RepRisk debt-share models do not require the correction. Table 5 reports the clustering, leave-one-year-out, and wild-bootstrap checks; the supplement reports the wider multiplicity calculations.

We report two further sensitivity calculations for the central ETI coefficient. Following Oster [29], short and full regressions use identical samples and the same fixed-effect transformation. One comparison adds lagged emissions and all six financial controls to an ETI-only regression; a second holds lagged emissions in both models and adds the six financial controls. We report signed values of the proportional-selection parameter for Rmax⁡=1.3Rfull2R_{\max} = 1.3R_{\mathrm{full}}^{2} and Rmax⁡=1R_{\max} = 1, because the result is sensitive to that choice. Following Frank [18], we also report the impact threshold for an omitted confounder and the corresponding equal partial correlations. The conventional formula does not directly accommodate two-way clustered inference, so this is reported as a sensitivity calculation rather than a formal clustered test.

We do not use the state-level ESG instrument. State ESG conditions can affect environmental policy, litigation, investors, banking conditions and debt markets directly, so its exclusion restriction is not credible. We also do not use extreme-quartile propensity-score matching as evidence about unobserved selection. Removing those analyses is preferable to retaining them with claims they cannot support.

Results

Sample coverage and measurement checks

Table 1 documents the movement from the 16,258-row master panel to the principal estimation samples and summarizes the main variables. Debt shares are observed for 15,912 firm-years. Exact lags, complete controls, and fixed-effect singleton removal leave 8,219 observations for the continuous ratio-free debt model and 8,242 for the quadrant model. The RepRisk debt model uses 10,373 observations. The simultaneous ten-measure comparison uses 8,061 observations. Facility-level spread tests are smaller: the continuous talk–emissions specification uses 1,946 facilities from 425 firms and eight outcome years. These differences make table-specific samples and cluster counts integral to interpretation.

ETI is available for 13,410 observations. It has a mean of 0.0030, a standard deviation of 0.0439, and an observed range from −1.1368-1.1368 to 1.5409. Appendix Table A1 reports its full empirical distribution and central mass, and Figure 1 plots the distribution. The ETI is much less dispersed than ratios computed directly from the available emissions and talk components. The source files do not establish why.

Figure 1. Distribution of the Emissions-to-Talk Index Notes: Panel A plots the empirical cumulative distribution over all 13,410 nonmissing observations on a symmetric-log horizontal scale; the dashed lines mark the 1st and 99th percentiles. Panel B displays the central 98 percent of the raw distribution and the corresponding fixed 1st/99th percentile winsorized distribution. The figure is descriptive.

The presentation-only comparison ratio has 9,519 nonmissing values, a standard deviation of approximately 1,604, and a range from approximately −8,117 to 69,705. The change-on-change ratio is more extreme: among 11,394 values its standard deviation is approximately 382,359 and its range extends from about −40.24 million to 2.62 million. Appendix Table A1 and Figure A1 show that these tails are not minor departures from normality. They follow mechanically when presentation talk or its change approaches zero.

Figure A1. Distributions of three emissions-to-talk ratios

Notes: The rows show the ETI, the presentation-only emissions-growth-to-talk ratio, and the emissions-change-to-talk-change ratio. Left panels plot empirical cumulative distributions on symmetric-log scales, with dashed lines at the 1st and 99th percentiles. Right panels show the central 98 percent of each raw distribution and its fixed 1st/99th percentile winsorized counterpart. The three ratios are shown in their raw units.

The distributional problem has empirical consequences. In the exact-lag comparisons, the untrimmed presentation-only ratio has no statistically detectable association with bank share in the firm-effect model, whereas its 1st/99th-percentile winsorized version has a positive coefficient. That direction is opposite to the monitoring-avoidance prediction. Other ratio estimates also change across tail-treatment rules and debt categories (Appendix Table A6). For this reason, statistical significance after a particular winsorization is not treated as confirmation. All central conclusions are based on components and quadrants that do not divide by talk.

The sample correlations in Appendix Table A2 support the same measurement distinction. Presentation talk is highly correlated with the Sautner overall exposure measure (Pearson correlation 0.966), as expected from shared dictionary content. That number shows that the field captures climate-related language. It cannot independently establish that the language is favorable, costly, or misleading. Correlations among RepRisk, LSEG, emissions, and debt fields are substantially less mechanical, which motivates the joint models rather than substituting one label for another.

Appendix Table A25 reports correlations among the ETI, log total emissions, presentation-plus-management-answer TalkFreq, the LSEG ESG and Emissions scores, firm size, and bank-debt share. The unconditional ETI–bank-share correlation is 0.004 (N=13,182N = 13{,}182; p=0.626p = 0.626). The TalkFreq variable in that table is the winsorized presentation-plus-management-answer measure; it is distinct from the presentation-only variable used in the ratio-free models.

Appendix Table A23 compares the ratio-free configurations with later RepRisk incidents as an outside check. The continuous talk–emissions interaction has no statistically detectable association with the logged greenwashing count (p=0.371p = 0.371), greenwashing incidence (p=0.567p = 0.567), or environmental incidents (p=0.579p = 0.579) in the firm-and-year models. The high-talk/rising-emissions category has a 1.39-percentage-point coefficient for greenwashing incidence (p=0.061p = 0.061), but the corresponding Holm value is 0.552. This is a directionally suggestive raw association, not multiplicity-adjusted evidence that the construction measures greenwashing.

Call segments and subsequent environmental information

Appendix Table A22 reports the segment-level comparisons with external outcomes. The presentation- and answer-section measures enter jointly, so each coefficient reports that segment’s association conditional on the other segment measure. The displayed columns include firm and year effects, lagged firm controls, the prior emissions state, and the lagged value of the outcome.

The presentation-section measure is positively associated with the next-year count of externally recorded greenwashing incidents. A one-standard-deviation increase in the transformed prepared-talk measure is associated with a 0.0096 increase in log⁡(1+n)\log(1 + n) greenwashing incidents (standard error 0.0024, p=0.002p = 0.002; N=10,512N = 10{,}512). The section-wide Holm value is 0.049. Answer talk has no statistically detectable association with the same outcome (β^=−0.0011\hat{\beta} = -0.0011, p=0.665p = 0.665).

The binary outcome points in the same direction but is weaker. Prepared talk is associated with a 0.75 percentage-point increase in the probability of at least one next-year greenwashing incident (standard error 0.33 percentage points, raw p=0.044p = 0.044). Its section-wide Holm value is 0.750. The count and incidence results point in the same direction, but the latter does not remain below conventional thresholds after the displayed adjustment.

The pattern is reversed for the broader environmental count. The answer-section measure is positively associated with next-year log⁡(1+n)\log(1 + n) environmental incidents after conditioning on the lagged count (β^=0.0107\hat{\beta} = 0.0107, standard error 0.0030, raw p=0.005p = 0.005). Its section-wide Holm value is 0.097. The presentation-section measure is smaller and statistically indistinguishable from zero (β^=0.0052\hat{\beta} = 0.0052, p=0.378p = 0.378). In these models, the presentation-section coefficient is statistically significant for the greenwashing-news count but not the broader environmental count. Because news coverage and underlying exposure can drive both, this remains an interpretation rather than an identified mechanism.

Neither segment is statistically associated with subsequent emissions change in the persistence model. The prepared-talk coefficient is 0.0038 (standard error 0.0053, p=0.498p = 0.498) and the answer-talk coefficient is 0.0027 (standard error 0.0030, p=0.395p = 0.395) in 8,388 observations. Table 2 separately reports the relation between presentation talk and cumulative emissions changes over one, two, and three years. The firm-effect coefficients are 0.0036, 0.0023, and 0.0002, with pp-values of 0.382, 0.661, and 0.981. Presentation talk is also unrelated to later emissions intensity (coefficient −0.0016-0.0016, p=0.757p = 0.757). Thus, we find no evidence that more climate language is systematically followed by either emissions abatement or increased emissions.

The segment results clarify what the fields capture; they do not establish a deception measure. Prepared language is positively associated with later externally recorded greenwashing news, but not with emissions change; answer language is associated with broader environmental news, but not greenwashing. The information source and the definition of the outcome matter. Prepared emphasis is associated with later negative-news records and may accompany latent exposure not captured by the controls. It would be an overreach to infer that the observed prepared passages contain false claims or that talk causes the later incident.

The ETI and debt composition

Table 3 reports the fixed-effect and timing comparisons; Appendix Table A3 gives the exact-lag results for all three debt shares. The first columns use the industry-and-year design. With lagged log emissions but no other controls, the ETI coefficient is −0.2265-0.2265 (standard error 0.0843; p=0.023p = 0.023; N=13,182N = 13{,}182). In the contemporaneous specification, adding the six financial controls reduces it to −0.0914-0.0914 (standard error 0.0380; p=0.037p = 0.037; N=10,691N = 10{,}691). This full industry-effect estimate remains economically modest: one standard deviation of ETI corresponds to roughly 0.4 percentage points of bank-debt share, compared with a mean share near 34 percent.

Baseline sampleCommon sampleExact lag
Industry/year parsimoniousIndustry/year full controlsIndustry/year full controlsFirm/year full controlsFirm/year full controls
ETI−0.2265<br>(0.0843)<br>p=.023p = .023−0.0914<br>(0.0380)<br>p=.037p = .037−0.0961<br>(0.0332)<br>p=.016p = .016−0.0178<br>(0.0517)<br>p=.738p = .7380.00159<br>(0.00297)<br>p=.606p = .606
Lagged log emissions includedYesYesYesYesYes
Six lagged firm controlsNoYesYesYesYes
Index timingttttttttt−1t - 1
Index scalingrawrawrawrawone SD
Observations13,18210,69110,48310,4838,334
Firms2,4762,0341,8261,8261,560
Year clusters1111111110
R2R^20.1710.2340.2390.7840.796
Within R2R^20.0650.1440.1480.0090.003

Table 3. Emissions-to-Talk Index and bank debt share

The firm-and-year model changes the result. On its available sample, the coefficient is −0.0178-0.0178 (standard error 0.0517; p=0.738p = 0.738; N=10,483N = 10{,}483). We also estimate both fixed-effect structures on exactly these 10,483 observations. The industry-and-year coefficient is then −0.0961-0.0961 (standard error 0.0332; p=0.016p = 0.016), while the firm-and-year coefficient is unchanged at −0.0178-0.0178. The reduction of about 81.5 percent therefore does not arise from sample composition or the observations dropped as firm-effect singletons. It arises when the comparison shifts from differences across firms within industries to changes within the same firm.

Appendix Table A14 makes the same distinction through a within–between decomposition on the 10,483-observation sample. The coefficient on the within-firm deviation is −0.0256-0.0256 (p=0.580p = 0.580), while the coefficient on the firm mean is −0.3068-0.3068 (p=0.222p = 0.222). Both are imprecise, but the contrast is consistent with the fixed-effect comparison: the data contain more of the negative relation in persistent differences across firms than in year-to-year changes within a firm.

ComponentCoefficientClustered SEppNN
Within-firm deviation−0.025570.04467.58010,483
Firm mean−0.306790.23543.22210,483

Table A14. Within- and between-firm decomposition of the ETI Notes: Both components enter a model with industry and year effects and the lagged controls. Standard errors are clustered by firm and year; pp-values use ten degrees of freedom. The covariance estimate required a positive-semidefinite safeguard. This decomposition is descriptive and does not replace the firm/year fixed-effect estimate.

The progression of controls is also informative. On the full industry-effect sample, an ETI-only model gives a coefficient of −0.0198-0.0198 (p=0.746p = 0.746). Adding lagged emissions makes the estimate −0.2328-0.2328 (p=0.004p = 0.004); adding the six financial controls then reduces its magnitude to −0.0914-0.0914. In the firm-effect sample, the corresponding coefficients are −0.0227-0.0227 (p=0.606p = 0.606), −0.0512-0.0512 (p=0.320p = 0.320), and −0.0178-0.0178 (p=0.738p = 0.738). Thus the negative industry-effect estimate is not an unconditional relation between ETI and bank share. It appears after conditioning on emissions and is then materially reduced by the financial controls. This pattern does not make the full model improper, but it shows why coefficient stability cannot be summarized by the final column alone.

Table 4 shows that the public-debt share offers no matching firm-effect result. In the industry-and-year model, ETI has a positive bond-share coefficient of 0.1234, but it is statistically imprecise (p=0.125p = 0.125). With firm and year effects the coefficient is 0.0028 (p=0.966p = 0.966). We report the residual other-debt share here; total-debt checks appear in Appendix Table A17. Because the three shares sum to one, a change in one category must be considered with the others. None of these regressions identifies a public bond issue or demonstrates improved access to the public market.

OutcomeIndustry + year FEFirm + year FENIYN_{IY}NFYN_{FY}FirmsIY_{IY}FirmsFY_{FY}
Bank debt share−0.0914<br>(0.0380)<br>p=.037p = .037−0.0178<br>(0.0517)<br>p=.738p = .73810,69110,4832,0341,826
Public bond debt share0.1234<br>(0.0736)<br>p=.125p = .1250.0028<br>(0.0633)<br>p=.966p = .96610,69110,4832,0341,826
Other debt share−0.0320<br>(0.0426)<br>p=.469p = .4690.0150<br>(0.0427)<br>p=.733p = .73310,69110,4832,0341,826

Table 4. ETI and the composition of debt

Timing provides a separate check. The variable ETIitETI_{it} uses emissions growth ending in tt and talk from t−1t - 1. Relating it to bank share in tt is therefore partly contemporaneous. When the completed index is lagged one more calendar year, the industry-and-year coefficient is −0.0163-0.0163, corresponding to a one-standard-deviation effect of −0.0007-0.0007, on a common 8,334-observation sample. Its unrepaired covariance has a positive diagonal and yields p=0.374p = 0.374, but the two-way covariance matrix is not positive semidefinite. The standard eigenvalue repair is sensitive to regressor scaling: estimating the raw-coordinate model and then rescaling its coefficient algebraically gives p=0.536p = 0.536, while standardized-coordinate implementations give values around 0.621–0.627. The firm-and-year coefficient is 0.0371, corresponding to a one-standard-deviation effect of 0.0016 (p=0.606p = 0.606). Appendix Table A4 reports exact-lag models that pair firm effects with two-digit SIC-by-year or state-by-year effects. The predictive specifications supply no evidence that ETI precedes a change in debt composition; this does not establish exogeneity.

Appendix Table A13 reports the Oster and Frank calculations, while Table 5 reports the covariance checks. The Oster result depends sharply on the assumed maximum R2R^2. In the firm-and-year model, holding lagged emissions in both the short and full specifications gives an exact signed δ\delta of 1.626 when Rmax⁡=1.3Rfull2R_{\max}=1.3R^2_{full}, but 0.0043 when Rmax⁡=1R_{\max}=1, using 10,483 observations. The corresponding industry-and-year values are 1.218 and 0.0616 on that model’s 10,691-observation sample. This variation is unsurprising in the firm-effect model because its within R2R^2 only rises from 0.00033 in the short model to 0.00867 in the full model, and the 1.3 rule sets Rmax⁡R_{\max} to just 0.01126. An ETI-only short model also produces signed values that change materially with the rule, including a negative value in the industry design because adding controls moves the coefficient away from zero. We report the full grid rather than selecting a single threshold.

PanelSpecificationCoefficientSEttppNNFirms
Panel A: covariance estimators
Industry/year FE: homoskedastic OLS−0.09138-0.091380.066390.06639−1.376-1.376.169.16910,69110,6912,0342,034
Industry/year FE: firm clusters−0.09138-0.091380.069660.06966−1.312-1.312.190.19010,69110,6912,0342,034
Industry/year FE: year clusters−0.09138-0.091380.055130.05513−1.657-1.657.128.12810,69110,6912,0342,034
Industry/year FE: firm + year clusters−0.09138-0.091380.037970.03797−2.407-2.407.037.03710,69110,6912,0342,034
Firm/year FE: firm + year clusters−0.01779-0.017790.051720.05172−0.344-0.344.738.73810,48310,4831,8261,826
Panel B: exact year-sign wild-cluster checks
Industry/year FE: year-studentized−0.09138-0.09138−1.657-1.657.250.25010,69110,6912,0342,034
Industry/year FE: resampled two-way statistic−0.09138-0.09138−2.407-2.407.122.12210,69110,6912,0342,034
Firm/year FE: year-studentized−0.01779-0.01779−0.337-0.337.743.74310,48310,4831,8261,826
Firm/year FE: resampled two-way statistic−0.01779-0.01779−0.344-0.344.732.73210,48310,4831,8261,826
Panel C: leave-one-year-out summary
Industry/year FE: range across 11 omissions[−0.1251,−0.0575][-0.1251,-0.0575]
Industry/year FE: omissions with p<.05p < .056 of 11
Firm/year FE: range across 11 omissions[−0.0740,0.0108][-0.0740,0.0108]
Firm/year FE: omissions with p<.05p < .050 of 11

Table 5. Inference and coefficient-sensitivity checks for the ETI model. Notes: All rows use the full model and its fixed-effect-specific estimation sample. The wild-cluster tests enumerate the 1,024 unique two-sided Rademacher sign assignments for 11 year clusters and impose the null. The year-studentized version is the preferred check with few year clusters; the resampled two-way statistic is also reported. In the industry/year model, the two-way variance is smaller than either one-way variance because the firm/year intersection component is subtracted. Leave-one-year-out pp-values use the remaining ten year clusters. These checks concern inference and temporal influence; they do not establish exogeneity.

Fixed effectsShort modelβ^S\hat{\beta}_{S}RS2R^{2}_{S}β^F\hat{\beta}_{F}RF2R^{2}_{F}Rmax⁡R_{\max}Exact δ(β∗=0)\delta(\beta^{*}=0)NN
Panel A: proportional-selection calculations using within-transformed quantities
Industry/yearIndex only−0.019800.000007−0.091380.1438220.186968−4.26710,691
Industry/yearIndex only−0.019800.000007−0.091380.1438221.000000−0.21610,691
Industry/yearIndex + lagged emissions−0.232830.061301−0.091380.1438220.1869681.21810,691
Industry/yearIndex + lagged emissions−0.232830.061301−0.091380.1438221.0000000.061610,691
Firm/yearIndex only−0.022740.000034−0.017790.0086650.0112655.81210,483
Firm/yearIndex only−0.022740.000034−0.017790.0086651.0000000.015310,483
Firm/yearIndex + lagged emissions−0.051160.000329−0.017790.0086650.0112651.62610,483
Firm/yearIndex + lagged emissions−0.051160.000329−0.017790.0086651.0000000.004310,483
Panel B: Frank impact-threshold calculation for the industry/year estimate
Rerun-result plug-in; conventional regression df = 10,608ITCV = 0.00442equal partial rr = 0.06645reference tt = 1.96019
Cluster-calibrated analogue; year-cluster df = 10ITCV = 0.06986equal partial rr = 0.26431reference tt = 2.22814

Table A13. Coefficient-selection calculations and Frank ITCV

Applying Frank’s published-results formula to the two-way-clustered tt-statistic, but using conventional regression degrees of freedom, gives a plug-in impact threshold of approximately 0.0044. This corresponds to equal conditional partial correlations of about 0.066 between an omitted variable and ETI and between that variable and bank share. A cluster-calibrated analogue using the year-cluster degrees of freedom is 0.0699, with equal partial correlations of about 0.264. Neither is an exact extension of the method to a two-way covariance. Under the homoskedastic OLS standard error for which the calculation was derived, the coefficient already has p=0.169p=0.169, so the orthodox threshold needed to make it statistically insignificant is zero. We treat the plug-in numbers as descriptive sensitivity statistics rather than corrections for omitted variables.

The covariance estimates explain why the pp-values differ. For the industry-and-year coefficient, the homoskedastic, firm-clustered, year-clustered and two-way clustered standard errors are 0.0664, 0.0697, 0.0551 and 0.0380. Their two-sided pp-values are 0.169, 0.190, 0.128 and 0.037. The two-way estimate is smaller because the firm–year intersection term subtracts most of the sum of the two one-way variance components. An exhaustive null-imposed year-sign bootstrap gives p=0.250p=0.250 when studentized with the year-cluster covariance and p=0.122p=0.122 when studentized with the two-way covariance. In leave-one-year-out models the industry coefficient is always negative but is below 5 percent in six of eleven cases; no firm-effect estimate is below 10 percent. These checks do not show that the industry-and-year coefficient is exactly zero. They show that it does not provide a secure basis for a causal monitoring account.

Ratio-free climate information and debt composition

Table A19 presents the principal financing results. The continuous model includes standardized presentation talk, standardized emissions change, and their product simultaneously. With firm and year effects, the bank-share coefficients are 0.0059 for emissions change (standard error 0.0031, p=0.092p=0.092), −0.0028 for presentation talk (standard error 0.0031, p=0.386p=0.386), and −0.0002 for their interaction (standard error 0.0011, p=0.865p=0.865). The three terms are jointly insignificant (p=0.307p=0.307), and the Holm values across the three debt outcomes are at least 0.828. The estimation sample contains 8,219 observations for 1,548 firms over ten outcome years.

OutcomeInformation term at t−1t - 1Firm + year FEIndustry + year FEHolm pFYp_{FY}NNFirms
Bank shareChange in log emissions0.0059 (0.0031) p=.092p = .0920.0049 (0.0051) p=.362p = .362.8288,2191,548
Bank sharePresentation climate talk−0.0028 (0.0031) p=.386p = .3860.0062 (0.0053) p=.270p = .2701.0008,2191,548
Bank shareTalk ×\times emissions change−0.0002 (0.0011) p=.865p = .8650.0026 (0.0029) p=.399p = .3991.0008,2191,548
Bond shareChange in log emissions−0.0022 (0.0047) p=.646p = .646−0.0017 (0.0059) p=.786p = .7861.0008,2191,548
Bond sharePresentation climate talk0.0013 (0.0035) p=.720p = .720−0.0067 (0.0062) p=.311p = .3111.0008,2191,548
Bond shareTalk ×\times emissions change0.0024 (0.0014) p=.129p = .129−0.0021 (0.0033) p=.531p = .5311.0008,2191,548
Other shareChange in log emissions−0.0037 (0.0029) p=.231p = .231−0.0032 (0.0029) p=.289p = .2891.0008,2191,548
Other sharePresentation climate talk0.0016 (0.0026) p=.568p = .5680.0005 (0.0044) p=.914p = .9141.0008,2191,548
Other shareTalk ×\times emissions change−0.0022 (0.0016) p=.192p = .192−0.0004 (0.0024) p=.856p = .8561.0008,2191,548

Table A19. Ratio-free continuous climate-information terms and debt composition. Notes: Continuous terms are scaled by one standard deviation. All information terms and rebuilt controls use exact calendar lags; the outcome is dated tt. The two fixed-effect designs use the same observations. Standard errors are clustered by firm and year and pp-values use nine degrees of freedom. For bank share, the three firm-effect information terms are jointly insignificant (p=.307p = .307). Holm pFYp_{FY} adjusts the nine firm-effect information coefficients displayed in the table; the smallest adjusted value is .828.

The quadrant specification in Appendix Table A21 reaches the same conclusion without imposing a linear interaction. Relative to low talk/non-rising emissions, the high-talk/rising-emissions coefficient for bank share is 0.0101 (standard error 0.0072, p=0.193p = 0.193). The high-talk/non-rising and low-talk/rising coefficients are also positive and individually insignificant, and the quadrant indicators are jointly insignificant (p=0.407p = 0.407). The high-talk/rising-emissions estimate therefore has the opposite sign from monitoring avoidance, but it is too imprecise to support a positive financing claim.

OutcomeConfiguration at t−1t-1Firm + year FEIndustry + year FEHolm pFYp_{FY}NNFirms
Bank shareHigh talk, non-rising emissions0.0064 (0.0053) p=.256p = .256−0.0016 (0.0118) p=.895p = .8951.0008,2421,551
Bank shareHigh talk, rising emissions0.0101 (0.0072) p=.193p = .193−0.0205 (0.0155) p=.217p = .2171.0008,2421,551
Bank shareLow talk, rising emissions0.0123 (0.0083) p=.172p = .172−0.0258 (0.0151) p=.121p = .1211.0008,2421,551
Bond shareHigh talk, non-rising emissions−0.0049 (0.0056) p=.403p = .4030.0020 (0.0143) p=.894p = .8941.0008,2421,551
Bond shareHigh talk, rising emissions0.0025 (0.0102) p=.815p = .8150.0333 (0.0148) p=.051p = .0511.0008,2421,551
Bond shareLow talk, rising emissions0.0046 (0.0073) p=.541p = .5410.0451 (0.0136) p=.009p = .0091.0008,2421,551
Other shareHigh talk, non-rising emissions−0.0015 (0.0053) p=.785p = .785−0.0004 (0.0060) p=.952p = .9521.0008,2421,551
Other shareHigh talk, rising emissions−0.0126 (0.0067) p=.094p = .094−0.0127 (0.0088) p=.184p = .184.7558,2421,551
Other shareLow talk, rising emissions−0.0169 (0.0072) p=.043p = .043−0.0193 (0.0084) p=.047p = .047.3858,2421,551

Table A21. Debt composition across ratio-free talk–emissions configurations. Notes: Low talk with non-rising emissions is the omitted configuration. Talk is split within two-digit SIC/year cells relative to the cell median among nonmissing presentation-talk values; cells require at least three observations. Rising emissions denotes a positive exact-calendar change. Information terms and rebuilt controls are dated t−1t-1. Designs use a common sample and firm/year clustered standard errors. For bank share, the three firm-effect configuration indicators are jointly insignificant (p=.407p = .407). Holm pFYp_{FY} adjusts the nine firm-effect configuration coefficients; none is below .10.

Bond and other-debt shares do not supply a coherent offset. There are isolated raw estimates, including a negative other-debt coefficient for the low-talk/rising-emissions category, but they are insignificant after the relevant family-wise adjustment. In the industry comparison, some quadrant coefficients for bond share are positive, while the same-sample firm-effect estimates are smaller and insignificant. Given that the three shares sum to one, selective emphasis on a single raw coefficient would be misleading. The component and quadrant models do not show that talk–emissions configurations predict a firm’s subsequent debt mix.

Appendix Table A6 reports reconstructed presentation-only and change-on-change ratios before and after fixed tail treatment. Their estimates change in magnitude and sometimes in direction. Together with the correctly timed ETI results in Table 3, this shows that the negative coefficient is confined to its contemporaneous industry-effect specification rather than appearing across reasonable ways of joining talk and emissions.

Exploratory heterogeneity

We examine whether the ETI association varies with product-market competition, financial health, information opacity, and the Paris Agreement period. An interaction in an observational debt-share regression does not identify monitoring avoidance. It may reflect borrower demand, lender supply, public-market access or another characteristic correlated with the moderator. We therefore describe these as exploratory comparisons, show both fixed-effect structures, and consider the number of related tests.

We do not report two further moderator splits. A state-political classification would raise the same state-level confounding concern as the instrument discussed above, and a bank-debt-level split conditions on a close relative of the outcome.

Product-market competition

A possible competition argument is that firms in more competitive markets may face stronger short-run pressure and therefore place greater weight on climate communication relative to operational change. A monitoring-avoidance account would then predict greater bank scrutiny and less borrower demand for bank debt. The first step is possible but not measured directly; the second cannot be inferred from an annual debt share. Product-market competition is itself related to debt choice and managerial incentives [5, 24]; these links need not operate through climate discussion.

Appendix Table A7 reports the competition tests. Low product substitutability, high industry concentration and a low number of competitors are defined relative to the sample median within the available variables. Each moderator, ETI and their interaction enter with the baseline controls. Under industry and year effects, the interaction coefficients are positive: 0.3035 for low substitutability, 0.3365 for high concentration and 0.4155 for few competitors. Their pp-values are 0.067, 0.007 and 0.004. These estimates imply that the negative ETI coefficient is weaker in less competitive settings.

With firm and year effects, the same interactions fall to 0.1204, 0.0738 and 0.1702, with pp-values of 0.348, 0.524 and 0.124. None is below the 5-percent threshold, and none provides strong evidence after adjustment across the competition family. In the exact-lag models reported in Appendix Table A10, all six competition interactions have raw pp-values above 0.54. The comparison suggests that the contemporaneous pattern largely reflects persistent differences across firms or industries.

Financial health

Financial condition can affect debt choice through several routes. A safer borrower may obtain public debt on better terms, but it may also retain bank relationships at lower cost. A constrained firm may value renegotiation and relationship capital, while a distressed firm may face restricted credit supply. Financial health can also affect environmental investment and the volatility of emissions. These competing channels make the interaction descriptive rather than a direct test of monitoring intensity.

Appendix Table A8 considers dividend payment, an above-median Altman Z-score and above-median market capitalization. The industry-effect interactions are positive, but none is individually statistically significant. With firm effects, the ETI–dividend interaction is 0.1766 (pp = 0.255), the ETI–high-market-value interaction is −0.0228 (pp = 0.795), and the ETI–high-Z interaction is 0.2091 (pp = 0.065). None crosses the 5-percent threshold even before accounting for the three related moderators, and the estimates sit beside statistically insignificant main ETI coefficients. We do not interpret the high-Z estimate as evidence that financial health weakens bank monitoring. In the exact-lag models, the firm-effect dividend and market-capitalization interactions have raw pp-values of 0.060 and 0.043, respectively, but both have within-family Holm values of 0.128 and their signs differ. This is not a common financial- health pattern.

Information opacity

Opacity is theoretically important but does not have a single implication for bank debt. Banks have an advantage over arm’s-length investors in producing private information (Fama, [14]; Krishnaswami et al., [26]), which may make bank debt more valuable to opaque firms. Poorer accounting quality is associated with more stringent private-debt terms (Bharath et al., [4]), while an informational advantage can strengthen lender bargaining power (Rajan, [30]). Changes in the information environment can also alter firms’ financing choices (Li et al., 2019). We consider four proxies: analyst forecast dispersion, low analyst coverage, a high bid–ask proxy, and high intangible intensity. These measures reflect different aspects of the information environment and none is treated as universally preferable.

Appendix Table A9 reports all four interactions. Under firm and year effects, the interaction pp-values are 0.275 for forecast dispersion, 0.030 for low coverage, 0.272 for the bid–ask proxy and 0.897 for intangibles. The low-coverage estimate is positive, but its Holm value across the four opacity tests is 0.120. The other three estimates are individually imprecise. We therefore do not find a consistent opacity pattern. The result also illustrates why the choice of a single proxy after inspection would be misleading: the only raw coefficient below 5 percent is not the bid–ask proxy. Rebuilding the moderator dummies so missing source observations remain missing and imposing exact timing changes the pattern. The high-intangibles interaction is positive with firm effects and has a raw pp-value of 0.0014 and a within-opacity Holm value of 0.0055. Its two-way covariance requires an eigenvalue correction that is sensitive to scaling; an exact year-sign check has p=0.043p = 0.043 before and 0.391 after adjustment across all ten exact-lag moderator tests. We therefore report the estimate but do not generalize it across the four opacity proxies.

High analyst dispersionLow analyst coverageHigh bid–ask proxyHigh intangibles
I/YF/YI/YF/YI/YF/YI/YF/Y
ETI0.01402<br>(0.16219)<br>p=.933p = .9330.08585<br>(0.10682)<br>p=.440p = .440−0.26307<br>(0.09793)<br>p=.023p = .023−0.21251<br>(0.07327)<br>p=.016p = .016−0.02742<br>(0.10898)<br>p=.806p = .8060.07990<br>(0.10609)<br>p=.469p = .469−0.09361<br>(0.05000)<br>p=.091p = .091−0.00956<br>(0.07350)<br>p=.899p = .899
Index × moderator−0.14943<br>(0.23965)<br>p=.547p = .547−0.14891<br>(0.12896)<br>p=.275p = .2750.31324<br>(0.16416)<br>p=.085p = .0850.34912<br>(0.13821)<br>p=.030p = .030−0.05738<br>(0.12797)<br>p=.663p = .663−0.10796<br>(0.09278)<br>p=.272p = .2720.01732<br>(0.08896)<br>p=.850p = .850−0.01930<br>(0.14567)<br>p=.897p = .897
Moderator0.00087<br>(0.01033)<br>p=.935p = .935−0.00471<br>(0.00745)<br>p=.541p = .5410.07435<br>(0.01348)<br>p<.001p < .0010.00211<br>(0.01435)<br>p=.886p = .8860.06925<br>(0.01267)<br>p<.001p < .0010.01854<br>(0.01051)<br>p=.108p = .1080.06291<br>(0.01952)<br>p=.009p = .0090.01206<br>(0.00993)<br>p=.252p = .252
Holm pp, interaction family1.000.816.340.1201.000.8161.000.897
Observations10,69110,48310,69110,48310,69110,48310,69110,483

Table A9. Information opacity: contemporaneous specification. Notes: I/Y and F/Y denote industry/year and firm/year fixed effects. These are contemporaneous specifications using the ETI and binary opacity moderators; missing inputs are coded as low opacity. We therefore treat this table as a sensitivity check and use Table A10, which leaves missing inputs missing, for the exact-lag comparison. All models include the full lagged control set and use two-way firm/year clustering. The Holm row adjusts the four interaction pp-values within each fixed-effect design. The low-coverage interaction has raw p=.030p = .030 with firm effects and adjusted p=.120p = .120. The source files do not document the construction of the bid–ask proxy. These four binary proxies do not cover every aspect of opacity.

Time pattern and the Paris Agreement

We divide the sample into years before 2016 and years from 2016 onwards. The split also coincides with changes in green-bond markets, environmental reporting, investor demand, regulation and the composition of firms covered by the linked databases. It is therefore not a Paris Agreement research design.

Appendix Table A11 retains the split. With industry and year effects, the pre-2016 ETI coefficient is −0.0079-0.0079 (p=0.980p = 0.980) and the post-2016 coefficient is −0.0949-0.0949 (p=0.032p = 0.032). With firm and year effects they are −0.0599-0.0599 (p=0.753p = 0.753) and −0.0168-0.0168 (p=0.750p = 0.750). The relevant question is not whether one coefficient crosses a threshold while another does not, but whether the two differ. The formal pre/post equality tests are statistically insignificant under both structures (p=0.783p = 0.783 for industry effects and p=0.812p = 0.812 for firm effects). The annual coefficients in Figure 2 also vary around zero and their 95-percent intervals overlap zero. These results do not support a discrete change after 2015. Exact-lag versions lead to the same conclusion whether the post period is dated by the debt-outcome year or the index source year; every pre/post equality-test pp-value exceeds 0.50.

Figure 2. Year-specific debt-composition estimates

Notes: Panel A reports year-specific industry-effect coefficients on the contemporaneous ETI with two-digit-industry fixed effects. Panel B reports descriptive annual slopes for the exact-lag ratio-free interaction in the pooled firm/year specification. Bars are 95 percent confidence intervals. The dotted line separates pre-2016 and later outcome years for visual reference; it is not an event-study estimate or a causal break test.

Industry + year FEFirm + year FE
Panel A: contemporaneous specification; split by outcome year
ETI × pre-2016−0.00785 (0.30553) p=.980p = .980−0.05987 (0.18470) p=.753p = .753
ETI × post-2016−0.09489 (0.03818) p=.032p = .032−0.01683 (0.05132) p=.750p = .750
Post minus pre−0.08704 (0.30744) p=.783p = .7830.04304 (0.17622) p=.812p = .812
Observations10,69110,483
Firms2,0341,826
R2R^20.23380.7837
Panel B: exact-lag model; split by outcome year
ETI × pre-20160.00241 (0.01967) p=.905p = .905−0.00432 (0.01115) p=.707p = .707
ETI × post-2016−0.00088 (0.00142) p=.552p = .5520.00200 (0.00318) p=.545p = .545
Post minus pre−0.00329 (0.01958) p=.870p = .8700.00632 (0.01176) p=.604p = .604
Observations8,3348,334
Firms1,5601,560
Panel C: exact-lag model; split by index source year
ETI × pre-20160.00616 (0.01697) p=.725p = .725−0.00401 (0.00860) p=.652p = .652
ETI × post-2016−0.00116 (0.00141) p=.432p = .4320.00204 (0.00322) p=.543p = .543
Post minus pre−0.00731 (0.01683) p=.674p = .6740.00605 (0.00936) p=.535p = .535
Observations8,3348,334
Firms1,5601,560

Table A11. Pre/post-2016 estimates and coefficient-equality tests. Notes: Panel A is the contemporaneous specification using the ETI and fixed-effect-specific samples. Panels B and C use the one-SD index from exact t−1t - 1, with the pooled exact-lag standard deviation 0.043628, rebuilt controls from exact t−1t - 1, and a common industry/firm-effects sample; outcome years 2016–2021 are post in Panel B. Panel C dates the split by the index source year, so the 2016 outcome is assigned to the pre period because its regressor comes from 2015. Standard errors are clustered by firm and year. Each difference is a linear contrast of the two slopes using their covariance. Industry/year covariances in Panels B and C require a positive-semidefinite repair; firm/year covariances do not. No equality test is below .50. Annual estimates for the contemporaneous specification appear in Figure 2, Panel A.

The heterogeneity results do not establish a monitoring mechanism. Several industry-effect patterns are present, but they do not form a coherent within-firm pattern once firm effects, common samples and the number of related tests are considered. This does not rule out variation in how firms and banks respond to climate information. It means that these moderators cannot identify that variation in the present panel.

Additional analyses

Comparison across information sources

Table A24 asks whether another climate field adds information about debt composition once the interaction and the other measures are included. Ten variables enter simultaneously: presentation talk, emissions change, their interaction, environmental incidents, a greenwashing indicator, Sautner opportunity, regulatory, and physical exposures, and LSEG ESG and Emissions scores. The common sample contains 8,061 observations for 1,529 firms over ten years.

Information at t−1t-1Bank shareBond shareOther shareHolm pp
Presentation climate talk−0.0024 (0.0032) p=.478p = .478−0.0001 (0.0035) p=.982p = .9820.0024 (0.0027) p=.383p = .3831.000
Change in log emissions0.0049 (0.0031) p=.156p = .156−0.0012 (0.0047) p=.809p = .809−0.0037 (0.0029) p=.236p = .2361.000
Talk × emissions change−0.0002 (0.0010) p=.829p = .8290.0025 (0.0015) p=.123p = .123−0.0022 (0.0015) p=.178p = .1781.000
RepRisk environmental incidents−0.0023 (0.0020) p=.281p = .2810.0009 (0.0035) p=.797p = .7970.0014 (0.0037) p=.719p = .7191.000
Any RepRisk greenwashing incident0.0029 (0.0058) p=.637p = .6370.0023 (0.0071) p=.754p = .754−0.0052 (0.0093) p=.593p = .5931.000
Sautner opportunity exposure−0.0046 (0.0069) p=.522p = .5220.0104 (0.0060) p=.118p = .118−0.0058 (0.0039) p=.176p = .1761.000
Sautner regulatory exposure0.0016 (0.0020) p=.432p = .432−0.0004 (0.0019) p=.840p = .840−0.0012 (0.0027) p=.658p = .6581.000
Sautner physical exposure0.0100 (0.0041) p=.039p = .039−0.0055 (0.0029) p=.088p = .088−0.0045 (0.0026) p=.120p = .1201.000
LSEG ESG score−0.0043 (0.0102) p=.680p = .6800.0088 (0.0162) p=.600p = .600−0.0045 (0.0115) p=.707p = .7071.000
LSEG Emissions score−0.0031 (0.0106) p=.776p = .7760.0077 (0.0119) p=.535p = .535−0.0046 (0.0081) p=.587p = .5871.000
Observations8,061
Firms1,529

Table A24. Joint regressions with climate-information measures Notes: All ten information measures enter simultaneously in each firm/year-effects regression. Continuous measures are standardized; any greenwashing is binary. Rebuilt controls and information measures use exact calendar lags. Standard errors are clustered by firm and year. Holm pp adjusts the 30 displayed information coefficients; every adjusted value equals one. The firm/year bank-share covariance required a positive-semidefinite repair; the bond- and other-share covariances did not.

For bank-debt share, the talk coefficient is −0.0024-0.0024 (p=0.478p = 0.478), the emissions-change coefficient is 0.00490.0049 (p=0.156p = 0.156), and their interaction is −0.0002-0.0002 (p=0.829p = 0.829). Environmental incidents are also insignificant in this restricted common sample (−0.0023-0.0023, p=0.281p = 0.281), as are the greenwashing indicator and both LSEG scores. The Sautner physical-exposure coefficient is 0.01000.0100 with a raw pp-value of 0.039. It is insignificant after adjustment across the displayed information coefficients; all Holm values in the joint comparison are one. The bank-share covariance required a positive-semidefinite repair, so the isolated raw coefficient warrants additional caution. No information measure remains significant in the analogous bond- and other-debt families.

In this restricted common sample, none of the measures has a statistically significant additional association with debt composition after conditioning on the others. This result does not imply that every measure is uninformative in other settings, and it does not show that the talk–emissions index measures the same object.

The segment-level results provide a useful contrast. Prepared talk has a forward association with an external greenwashing count, yet it does not explain the debt mix. A measure can be associated with an external outcome without lenders or borrowers responding in a way detectable in annual debt shares. Conversely, the Sautner topical exposures and LSEG scores need not reproduce findings from other samples or outcomes. Exposure, rating coverage, score levels, and negative news answer different questions.

External controversies and bank-debt share

Appendix Table A12 begins with externally recorded events rather than managerial language. In the model that includes standardized environmental incidents and the greenwashing indicator, a one-standard-deviation increase in the environmental count at t−1t - 1 is associated with a 0.61-percentage-point decrease in bank share at tt (coefficient −0.0061-0.0061, standard error 0.0023, raw p=0.023p = 0.023; N=10,373N = 10{,}373). The greenwashing indicator has no statistically detectable association with bank share (coefficient −0.0016-0.0016, p=0.835p = 0.835). In a separate model, a one-standard-deviation increase in total ESG incidents is associated with a 1.13-percentage-point decrease in bank share (coefficient −0.0113-0.0113, standard error 0.0047, raw p=0.039p = 0.039).

The magnitude is modest relative to an average bank share near 34 percent, and specificity checks narrow the interpretation. When environmental incidents are conditioned on total incident activity and the greenwashing indicator, the displayed environmental coefficient falls to −0.0016-0.0016 (p=0.550p = 0.550). The broad total-incident measure is associated with bank share when estimated separately, whereas greenwashing-specific measures remain statistically insignificant.

The environmental estimate is suggestive before adjustment but not after accounting for the testing family. The exactly enumerated one-way year-cluster wild-bootstrap gives p=0.024p = 0.024. Yet the Holm value across the six selected wild-bootstrap checks is 0.141, and the one-way bootstrap omits within-firm dependence. In the broad primary testing family, the adjustment is larger still.

Appendix Table A26 reports lead–lag estimates. In a common 6,526-observation distributed model with firm and year effects, the lagged environmental coefficient is −0.0042 (p=0.227p = 0.227), the current-event coefficient is 0.0013 (p=0.769p = 0.769), and the future-event coefficient is −0.0062 (p=0.330p = 0.330). None is individually significant. A descriptive first-event model similarly fails to support a causal interpretation: although individual within-firm pre-event coefficients are imprecise, their pre-event joint test rejects at the 5 percent level. Incident timing is therefore not a credible quasi-experiment in this panel.

We conclude that broad controversy activity may contain financing information that the internal talk–emissions measures do not. The data do not establish that the association is environmental rather than a manifestation of general reputation or governance risk. They also cannot distinguish firms choosing less bank debt from banks supplying less credit. The absence of a greenwashing-specific coefficient is particularly important: the prepared-talk result for subsequent news does not translate into a greenwashing-specific bank-share result.

Alternative measures and specification checks

Appendix Table A5 reports three further constructions. The first replaces presentation-plus-management-answer talk in the ETI denominator with the presentation-only frequency. This addresses the concern that an answer may be prompted by an analyst, but it does not resolve the small-denominator problem or show that a prepared passage contains a commitment. Its bank-share coefficient is just above the 5-percent threshold in the industry-effect model (p=0.053p = 0.053) and statistically insignificant with firm effects (p=0.731p = 0.731).

The second divides the change in log emissions by the change in presentation talk. This places changes in both numerator and denominator, but there is no economic reason to expect proportional changes in these two objects, and the ratio is undefined when talk does not change. Its raw distribution ranges from approximately −40.24 million to 2.62 million in the units used in the data. The industry-effect coefficient is positive (p=0.013p = 0.013), opposite to the ETI sign, and becomes statistically insignificant with firm effects (p=0.818p = 0.818). Winsorization changes its scale and can alter its sign. Using changes in both numerator and denominator does not by itself make the ratio economically preferable, so we treat it as a sensitivity check.

The third is an industry-year adjusted, standardized sum of presentation talk and emissions intensity. It avoids division and is defined when talk is zero, but it imposes an equal-weight aggregation whose economic meaning differs from ETI. Its coefficient is statistically insignificant with both industry effects (p=0.539p = 0.539) and firm effects (p=0.485p = 0.485). The component and quadrant results reported earlier are easier to interpret than this composite and therefore receive more weight. We also compare the component measures with LSEG ESG and Emissions scores and with the Sautner opportunity, regulatory, and physical exposure measures. The ten-variable comparison in Table A24 leaves every coefficient statistically insignificant after the declared family-wise adjustment. These findings do not show that the external measures are uninformative in general. They show that ETI is not a simple substitute for them and that none has a statistically significant additional association with annual debt shares after conditioning on the other measures in the common sample.

As further score and common-shock checks, Appendix Table A18 adds current or lagged LSEG ESG and Emissions scores and absorbs two-digit SIC-by-year effects. The industry-design ETI coefficients remain negative in these specifications, whereas the corresponding firm-design coefficients are small and statistically imprecise. Industry-by-year effects do not replace firm effects; they absorb a different set of common shocks. These columns do not change the conclusion that the within-firm and predictive ETI estimates are statistically indistinguishable from zero.

DealScan evidence from unique facilities

Table 6 evaluates the ETI in the one-record-per-facility file over complete years 2010–2019, holding the sample fixed across fixed-effect designs and clustering by firm and year. In the contemporaneous comparison, the one-standard-deviation ETI coefficient for the log all-in-drawn spread is 0.0473 (p=0.115p = 0.115) with industry and year effects and 0.0039 (p=0.883p = 0.883) with firm and year effects. With the index lagged by one calendar year, the coefficients are 0.0054 (p=0.749p = 0.749) and −0.0304 (p=0.169p = 0.169), respectively. All four estimates are statistically indistinguishable from zero, and their magnitudes vary with timing and fixed effects.

(1)(2)(3)(4)
Fixed effectsIndustry/yearFirm/yearIndustry/yearFirm/year
Index timingttttt−1t-1t−1t-1
Emissions-to-Talk Index, one SD0.047350.04735<br>(0.02674)(0.02674)<br>p=.115p=.1150.003870.00387<br>(0.02558)(0.02558)<br>p=.883p=.8830.005380.00538<br>(0.01618)(0.01618)<br>p=.749p=.749−0.03043-0.03043<br>(0.01985)(0.01985)<br>p=.169p=.169
Facility and firm controlsFullFullFullFull
Common sample within timingYesYesYesYes
Observations2,5072,5071,9881,988
Firms525525433433
Year clusters9988

Table 6. Loan spreads and the Emissions-to-Talk Index on unique DealScan facilities. Notes: The outcome is the log all-in-drawn spread on accepted facilities in the one-record-per-facility file, restricted to complete years 2010–2019. The Emissions-to-Talk Index is standardized over the master firm–years; columns 1–2 use the contemporaneous index and columns 3–4 an exact one-calendar-year lag. Facility controls are log amount, log maturity and security; firm controls are log assets, debt/assets, profitability, Altman Z-score and Tobin’s Q. Unknown security status is treated as missing. The sample is held fixed across the two fixed-effect designs within each timing, and standard errors are clustered by firm and year, with pp-values based on the number of year clusters minus one. Both exact-lag covariance matrices required a positive-semidefinite repair; neither contemporaneous covariance did. The contemporaneous coefficient is smaller with firm effects, but none of the four estimates is statistically distinguishable from zero. Accepted-facility spreads cannot separate loan demand from loan supply.

Appendix Table A15 examines appearance and volume in the linked extract. Industry-effect coefficients are positive for any matched facility, facility count, and reported amount, with raw pp-values of 0.023, 0.044, and 0.019. The corresponding firm-effect coefficients are near zero, with pp-values of 0.942, 0.785, and 0.928. These outcomes measure what is linked in DealScan; a non-match does not mean that a firm obtained no bank credit elsewhere.

The accepted-facility terms do not yield a matching pattern. Appendix Table A16 reports firm-effect coefficients of 0.018 (p=0.334p = 0.334) for the number of financial covenants, −0.014 (p=0.138p = 0.138) for security, and 0.007 (p=0.544p = 0.544) for log maturity. These contemporaneous specifications use firm-clustered standard errors and the available contract sample. The ratio-free facility tests in Appendix Tables A27 and A29 are also mixed: the continuous interaction is statistically insignificant for spread, security, and covenants, while isolated maturity and revolver coefficients do not remain below conventional thresholds after adjustment across the displayed facility outcomes. A high-talk/rising-emissions category likewise gives no common firm-effect pattern across incidence, pricing, maturity, security, and covenants.

Lagged RepRisk environmental incidents and the greenwashing indicator also fail to yield a coherent contract pattern. In the firm-effect models, neither measure is statistically associated with spread, maturity, security, covenants, revolver status, or facility incidence after the relevant outcome-family adjustment (Appendix Tables A27 and A28). Supplementary controls for loan type, deal purpose, and currency, and a U.S.-dollar subsample, do not reveal a common adverse-pricing relation (Appendix Table A29).

These findings should not be read as evidence that banks ignore climate information. The extract has neither rejected applications nor lender identities, lender environmental characteristics, green-loan flags, or complete bilateral lending. It also conditions facility-term equations on selection into an accepted syndicated deal. The available loan outcomes do not support a consistent screening, monitoring-avoidance, or favorable-access interpretation of the annual talk–emissions measures.

Total debt, annual stability, and further inference checks

Appendix Table A17 tests whether the share results mask changes in the total-debt denominator. The talk–emissions interaction has no statistically detectable association with log total debt (coefficient 0.0023, p=0.651p = 0.651) or rebuilt total debt-to-assets (coefficient −0.0001, p=0.916p = 0.916). The high-talk/rising category also has no statistically detectable association with either outcome. Environmental incidents have a raw coefficient of 0.0047 on debt-to-assets (p=0.054p = 0.054), while their log-total-debt coefficient is 0.0038 (p=0.696p = 0.696). The greenwashing indicator is insignificant for both. These regressions do not identify component amounts, but they provide no evidence that a consistent total-borrowing response underlies the statistically insignificant debt-share estimates.

Figure 2 examines year-specific stability. Panel A plots annual industry-effect coefficients for contemporaneous ETI with two-digit industry effects; firm effects are undefined within a one-year cross-section. Panel B plots descriptive year-specific slopes for the ratio-free interaction in the pooled firm-and-year specification with firm-clustered confidence intervals. The estimates vary around zero, and every 95 percent confidence interval includes zero. The ETI estimate is most negative in 2014 and has its smallest raw pp-value in 2017 (p=0.065p = 0.065), but no annual 95 percent confidence interval excludes zero. The ratio-free interaction likewise shows no stable pre/post-2016 change. The figure is not a Paris Agreement event study and does not support a structural-break claim.

Table 5 and Appendix Table A20 bring together the sensitivity results. The exact year-cluster wild-bootstrap pp-values are 0.852 for the interaction and bank share, 0.117 for the high-talk/rising bank-share contrast, 0.024 for environmental incidents and bank share, 0.045 for high-talk/rising emissions and future greenwashing incidence, 0.242 for the interaction and facility spread, and 0.023 for high-talk/rising emissions and facility count. None is significant after Holm adjustment across the six checks; the smallest adjusted value is 0.141. The bootstrap results support the same distinction: the central talk–emissions financing terms remain statistically insignificant, while a few external or secondary outcomes remain suggestive but cannot support broad claims.

Discussion

What the comparison reveals

The results show that climate information is source-dependent. The presentation- and answer-section measures are positively related to different future RepRisk categories. The two segment measures are not similarly related to later emissions changes, and none of the internal talk–emissions configurations is consistently related to debt composition. Broad external controversy counts exhibit a modest bank-share relation that is not greenwashing-specific. The differences indicate that words, operational outcomes, vendor scores, topical exposures, and negative news capture different information sets.

This distinction helps reconcile our evidence with recent work. Studies of climate exposure report greater bank reliance and interpret it as consistent with the value of flexibility and monitoring ([1]); studies of negative ESG news can find a shift toward public bonds ([28]). A climate word-frequency interaction need not reproduce either result. Similarly, evidence that adverse climate news affects loan terms ([22]) does not imply that prepared talk or an emissions ratio will do so. The empirical content of a variable follows from its construction and source, not the breadth of the label “climate risk.”

One exploratory result is the positive association between the presentation-section measure and the later count of greenwashing news, but it must be interpreted carefully. The measure precedes the count of greenwashing news even after prior incidents and the answer-section measure are included. This may reflect information common to the presentation field and later negative-news coverage. It is also consistent with omitted exposure, visibility, stakeholder attention, or contemporaneous initiatives that raise both prepared discussion and later news coverage. Without the underlying sentences and commitments, the result cannot distinguish a misleading claim from legitimate discussion of a difficult transition.

The answer-section result calls for the same caution. If the segment assignment is accurate, the field partly reflects an interactive exchange rather than a purely firm-initiated script. Its relation with broad environmental incidents may arise because already-exposed firms receive more attention. It would be inappropriate to describe the answer-section measure as independently verified voluntary disclosure.

Implications for debt-choice interpretation

Introducing firm effects changes both the ETI estimate and its debt-choice interpretation. The industry-effect coefficient compares firms that differ persistently in technology, disclosure, market access, and financing policy. Firm effects ask whether a given firm’s later debt share changes when its own information measure changes. The latter estimate is near zero for the ETI and for the ratio-free alternatives. It is therefore not defensible to infer that managers dynamically avoid bank scrutiny from the industry-and-year coefficient.

The sign ambiguity is not merely econometric. Monitoring can be costly to borrowers, but it can also be valuable when risk is complex and renegotiation is important. Bank screening and borrower avoidance produce the same negative share sign, while monitoring value can produce the opposite sign. Our loan tests were designed to seek additional observable implications, yet their isolated maturity, revolver, and facility-count estimates do not form a consistent pattern. A realized share plus mixed accepted-loan terms cannot identify which side of the market moved.

External controversies may matter differently because they are public negative signals rather than combinations of a firm’s own words and a vendor emissions field. The separate environmental and total-incident estimates resemble the direction documented for broader reputation risk [28]. However, their overlap and lack of greenwashing specificity, together with the weak lead–lag results for the environmental estimate, prevent a claim that banks respond to a particular environmental-controversy shock. General reputation risk, business deterioration, public-market activity, or changing financing demand can all produce the association.

Relevance for financial stability

The financial-stability implication is about information quality and model risk, not a demonstrated systemic effect. Credit institutions and supervisors often face pressure to summarize heterogeneous climate information in tractable scores. Ratios are attractive because they appear to compare words with outcomes. Here, small denominators create enormous values, tail treatment changes results, and the negative industry-and-year association loses statistical significance with an exact one-calendar-year lag and within-firm estimation. A mechanically constructed score can therefore look precise while remaining economically ambiguous.

Our evidence does not establish that the observed associations affect bank losses, fire-sale risk, credit supply over a cycle, or aggregate stability. It illustrates a measurement-risk concern for institution-level risk assessment: a volatile measure could be used to sort borrowers or enter stress models even when its within-firm financing content is negligible. Assessing such measures requires documented units and timing, attention to the differences between sources, denominator checks, and an assessment of out-of-sample or forward predictive content before interpreting them as risk measures.

Limitations

Six limitations define the scope of the conclusions. First, the available data contain annual precomputed transcript measures rather than raw calls and upstream extraction code. We can distinguish presentation and answer segments, preserve zeros, and state our subsequent transformations. We cannot verify every speaker classification, bigram denominator, quarterly weight, or omitted call, nor can we classify sentence valence. The segment associations should therefore be interpreted at the level of the available fields.

Second, the LSEG/Refinitiv emissions panel does not provide complete reported-versus-estimated flags, original publication dates, or historical vintages. Scope-specific coverage is sparse relative to the total field, and exactly unchanged annual totals are common. Calendar lags prevent use of future rows, but they cannot ensure that every vendor value was available in the same form at the relevant historical date.

Third, RepRisk incidents are event-based negative-news measures. Media visibility, geography, firm size, and provider coverage can affect recording. The greenwashing label is closer to the construct of misleading environmental communication than a talk–emissions ratio, but it is still neither a court finding nor a complete census. Predicting a RepRisk count can reflect future scrutiny as well as underlying conduct.

Fourth, debt shares do not retain the associated bank, bond, and other-debt amounts. We cannot identify green-bond issuance, sustainability-linked loans, ratings, or issuance opportunities. Although the total-debt checks help, a share movement cannot be assigned to a numerator or denominator component. The sample comprises public firms covered by the linked databases: the location field is incomplete and includes Canadian provinces, so the data do not support an exclusively U.S.-domiciled claim.

Fifth, the DealScan data observe accepted syndicated facilities, not applications, withdrawn deals, rejections, or all bilateral credit. They lack lender identifiers and lender climate characteristics in the DealScan extract. The file is incomplete after mid-July 2020 and absent in 2021, and several contract fields sharply reduce the usable sample. Unknown collateral status is left missing in the principal loan analyses. These features prevent us from separating demand from supply.

Sixth, the panel has only eight to eleven outcome-year clusters in key models. Two-way clustering, exact year-cluster wild-bootstrap enumeration, leave-one-year-out estimates, and family-wise adjustments expose this weakness but do not create additional independent time variation. Several raw results are sensitive to the testing family, and the one-way bootstrap cannot simultaneously model firm dependence. All estimates are conditional associations; none should be interpreted as a causal effect of talk, emissions, or incidents on financing.

These limitations restrict what can be learned from the available data. Within those limits, the paper reports statistically insignificant within-firm estimates, checks on the denominators, differences between the two call segments, and differences between internal and external measures.

Conclusion

This paper asks which forms of climate information are associated with corporate debt composition across the reported specifications. The answer depends sharply on what is measured. In exploratory tests, the presentation-section measure has a small positive association with the next-year count of externally recorded greenwashing news, while the answer-section measure has different content for broader environmental incidents. Neither segment measure is statistically associated with later emissions growth. The segment fields have limited predictive associations with later RepRisk incidents, but word frequency is not a promise, a costly signal, or proof of misleading conduct.

Outside the contemporaneous industry-and-year ETI benchmark, the principal financing estimates are statistically insignificant. Presentation talk, emissions change, their interaction, and complete talk–emissions quadrants do not consistently predict subsequent bank, bond, or other-debt shares within firms. The negative ETI relation appears only in the contemporaneous industry-effect specification; it is statistically insignificant with firm effects and is not recovered when the completed index is correctly lagged. Its one-standard-deviation magnitude in the former model is about 0.4 percentage points. Ratio tails and trimming sensitivity explain why ratio-free constructions should carry the main weight.

External controversies contain somewhat different information. Lagged environmental and total RepRisk counts have modest negative bank-share associations in separate raw tests. The result is not greenwashing-specific; the environmental association loses magnitude and statistical significance when total incidents enter, and wider-family multiplicity adjustment weakens both associations. The lead–lag estimates further weaken the environmental result. DealScan outcomes provide no consistent accompanying pattern in facility incidence, pricing, maturity, security, covenants, or revolver status. The data therefore do not establish that borrowers avoid monitoring or that banks ration firms on the basis of the measures studied here.

For research and financial-stability practice, the evidence calls for careful measurement. Earnings-call language, operating emissions, topical exposure, vendor scores, and external negative news should not be collapsed under a common credibility label without construct-specific evidence. Explicit timing, within-firm comparisons, denominator checks, and outcome-family inference materially change the conclusion. Better evidence on sentence-level commitments, historical-vintage emissions, issue-level debt, loan applications, and lender characteristics may reveal financing responses that the present data cannot identify. With the information available here, estimated associations with debt composition depend on the source and construction of climate information, and ETI has no consistent incremental association with debt composition.

Tables

Notes: The dependent variable is bank debt divided by total debt. The ETI for year tt already combines the emissions change ending in tt with talk measured before that change. Columns 1–4 relate debt composition in tt to this value; column 5 imposes an additional exact one-year lag and therefore relates debt composition in tt to the ETI dated t−1t - 1. Column 1 includes only the index and lagged emissions. Full models add lagged assets, debt/assets, tangibility, profitability, Tobin’s Q and Altman Z-score. Columns 3 and 4 use exactly the same observations. Standard errors are clustered by firm and year; pp-values use the number of year clusters minus one. Column 5 reports a one-standard-deviation effect from the native-coordinate exact-lag fit. The industry/year exact-lag estimate is −0.00070 (native-coordinate p=.536p = .536); because its two-way covariance is not positive semidefinite, alternative coordinate and unrepaired calculations give pp-values from .374 to .627. The firm/year estimate shown in column 5 is stable to this issue. The common-sample contemporaneous estimate falls by 81.5% when firm effects replace industry effects.

Notes: All three outcomes are proportions of total debt and sum to one. Models use the contemporaneous ETI, the full lagged control set, year effects and the fixed effects indicated. Standard errors are clustered by firm and year; unadjusted pp-values use 10 degrees of freedom. Other debt is calculated as one minus the bank and bond shares. These share regressions do not identify public-bond issuance, green instruments, or the direction of borrower and lender decisions.

Figures

Supplementary tables and figures

(1)(2)(3)(4)(5)(6)(7)(8)
(1) Presentation climate talk1.000−0.0470.1840.0540.8330.1510.220−0.037
(2) Change in log emissions−0.0171.000−0.075−0.042−0.054−0.089−0.1020.012
(3) RepRisk environmental incidents0.100−0.0261.0000.4020.1820.3580.405−0.226
(4) RepRisk greenwashing incidents0.055−0.0150.7241.0000.0500.2220.218−0.132
(5) Sautner overall climate exposure0.966−0.0180.1040.0591.0000.1420.220−0.029
(6) LSEG ESG score0.098−0.0470.2390.1830.1061.0000.795−0.220
(7) LSEG Emissions score0.141−0.0580.2360.1670.1490.8331.000−0.226
(8) Bank debt share−0.0700.006−0.131−0.096−0.068−0.265−0.2791.000

Table A2. Pairwise correlations among principal climate-information measures. Notes: Pearson correlations are below the diagonal and Spearman rank correlations are above it. Pairwise NN ranges from 13,180 to 16,258. The corresponding source file contains exact pp-values and pairwise observation counts. The 0.966 Pearson correlation between presentation talk and Sautner overall exposure reflects their closely related climate dictionaries, so the correlation does not provide an independent comparison of the two measures.

Fixed effectsOne-SD estimateClustered SEppNNFirms
Panel A: four-design common sample
Industry + year−0.0006410.001408.6608,2161,546
Firm + year0.0018440.003018.5568,2161,546
Firm + two-digit SIC ×\times year0.0015120.002974.6238,2161,546
Firm + state ×\times year0.0014770.002514.5718,2161,546
Panel B: each richer design’s available sample
Firm + two-digit SIC ×\times year0.0013360.002954.6628,2771,554
Firm + state ×\times year0.0011910.002599.6578,2781,552

Table A4. Exact-lag index under additional common-shock fixed effects

Notes: The bank debt share is dated tt; the ETI and rebuilt controls are exact calendar lags. One-SD effects use the pooled exact-lag index standard deviation, 0.043628; this differs from the estimation-sample standard deviation used in Table A3. Standard errors are clustered by firm and year and use nine degrees of freedom. Panel A holds observations fixed across all four designs. State-by-year effects absorb state-specific common shocks; they are not a political instrument and do not supply a source of exogenous variation. None of the richer fixed-effect estimates is statistically distinguishable from zero.

OutcomeIndustry + year FEFirm + year FENNFirmsYears
Bank debt share−0.00070 (0.00108) p=.536p = .5360.00159 (0.00297) p=.606p = .6068,3341,56010
Public bond debt share0.00020 (0.00305) p=.950p = .950−0.00024 (0.00322) p=.943p = .9438,3341,56010
Other debt share0.00050 (0.00235) p=.837p = .837−0.00135 (0.00234) p=.578p = .5788,3341,56010

Table A3. Exact-lag ETI and debt shares. Notes: The raw ETI is lagged by exactly one calendar year; coefficients and standard errors from the native-coordinate regressions are then multiplied by the estimation-sample SD, 0.042737. Both fixed-effect specifications use the same observations, rebuilt lagged controls and two-way firm/year clustering. pp-values use nine degrees of freedom. The industry/year covariance for the bank and other-debt models is not positive semidefinite and requires an eigenvalue repair. For the bank-share model, alternative coordinate and unrepaired calculations give pp-values from .374 to .627; .536 is the native-coordinate result. The firm/year results are stable. This table changes timing relative to the contemporaneous specification and is a predictive-timing check rather than a direct coefficient comparison.

MeasureIndustry + year FEFirm + year FENIYN_{IY}NFYN_{FY}FirmsIY_{IY}FirmsFY_{FY}
ETI−0.09138 (0.03797) p=.037p = .037−0.01779 (0.05172) p=.738p = .73810,69110,4832,0341,826
Presentation-only emissions/talk ratio−3.37 ×10−6\times10^{-6} (1.53 ×10−6\times10^{-6}) p=.053p = .053−4.54 ×10−7\times10^{-7} (1.29 ×10−6\times10^{-6}) p=.731p = .7317,8227,4821,8511,511
Change in emissions/change in talk3.76 ×10−9\times10^{-9} (1.25 ×10−9\times10^{-9}) p=.013p = .0132.71 ×10−10\times10^{-10} (1.15 ×10−9\times10^{-9}) p=.818p = .8189,2489,0071,9251,684
Standardized talk–emissions decoupling score0.00283 (0.00444) p=.539p = .539−0.00210 (0.00290) p=.485p = .48510,47110,2622,0011,792

Table A5. Alternative talk–emissions constructions and bank debt share

Notes: The dependent variable is the bank debt share. All rows use the full lagged control set and contemporaneous measures, year effects, the indicated fixed effects, and two-way firm/year clustering. The ratio measures are reported in their raw units, whereas the decoupling score is standardized. The change/change construction checks sensitivity to using changes in both components. Its denominator can be close to zero, and the sign of the ratio depends on whether talk rises or falls. The specifications therefore assess sensitivity to construction and should not be ranked by statistical significance.

OutcomeAlternative measure at t−1t - 1Firm + year FEIndustry + year FEHolm pFYp_{FY}NN
Bank shareChange/change ratio−0.0371-0.0371 (0.03570.0357); p=.325p = .325−0.1372-0.1372 (0.07200.0720); p=.089p = .089.325.3257,1977{,}197
Change/change ratio, winsorized−0.0017-0.0017 (0.00170.0017); p=.349p = .349−0.0030-0.0030 (0.00330.0033); p=.390p = .3901.0001.0007,1977{,}197
Presentation-only ratio0.00130.0013 (0.00200.0020); p=.518p = .518−0.0033-0.0033 (0.00250.0025); p=.221p = .221.717.7175,9295{,}929
Presentation-only ratio, winsorized0.00810.0081 (0.00220.0022); p=.005p = .0050.00140.0014 (0.00490.0049); p=.781p = .781.016.0165,9295{,}929
ETI0.00160.0016 (0.00300.0030); p=.606p = .606−0.0007-0.0007 (0.00140.0014); p=.626p = .6261.0001.0008,3348{,}334
ETI, winsorized0.00690.0069 (0.00310.0031); p=.054p = .0540.00140.0014 (0.00590.0059); p=.816p = .816.162.1628,3348{,}334
Bond shareChange/change ratio−0.0685-0.0685 (0.04420.0442); p=.155p = .155−0.0778-0.0778 (0.09860.0986); p=.450p = .450.311.3117,1977{,}197
Change/change ratio, winsorized0.00010.0001 (0.00170.0017); p=.969p = .9690.00140.0014 (0.00370.0037); p=.716p = .7161.0001.0007,1977{,}197
Presentation-only ratio0.00240.0024 (0.00250.0025); p=.359p = .3590.00110.0011 (0.00170.0017); p=.543p = .543.717.7175,9295{,}929
Presentation-only ratio, winsorized−0.0009-0.0009 (0.00210.0021); p=.679p = .6790.00750.0075 (0.00420.0042); p=.109p = .109.679.6795,9295{,}929
ETI−0.0002-0.0002 (0.00330.0033); p=.943p = .9430.00020.0002 (0.00310.0031); p=.950p = .9501.0001.0008,3348{,}334
ETI, winsorized−0.0020-0.0020 (0.00380.0038); p=.602p = .6020.00260.0026 (0.00540.0054); p=.643p = .643.602.6028,3348{,}334
Other-debt shareChange/change ratio0.10560.1056 (0.05320.0532); p=.078p = .0780.21500.2150 (0.05610.0561); p=.004p = .004.234.2347,1977{,}197
Change/change ratio, winsorized0.00160.0016 (0.00180.0018); p=.405p = .4050.00160.0016 (0.00170.0017); p=.367p = .3671.0001.0007,1977{,}197
Presentation-only ratio−0.0038-0.0038 (0.00170.0017); p=.052p = .0520.00220.0022 (0.00230.0023); p=.359p = .359.157.1575,9295{,}929
Presentation-only ratio, winsorized−0.0072-0.0072 (0.00260.0026); p=.021p = .021−0.0089-0.0089 (0.00270.0027); p=.009p = .009.042.0425,9295{,}929
ETI−0.0014-0.0014 (0.00240.0024); p=.578p = .5780.00050.0005 (0.00250.0025); p=.843p = .8431.0001.0008,3348{,}334
ETI, winsorized−0.0048-0.0048 (0.00290.0029); p=.133p = .133−0.0040-0.0040 (0.00420.0042); p=.362p = .362.265.2658,3348{,}334

Table A6. Exact-lag ratio tail checks and debt composition

Notes: Each ratio is standardized before its exact one-calendar-year lag is taken. The presentation-only and change/change rows use the rebuilt exact-calendar fields rather than the alternative-measure fields summarized in Table A1. Winsorized variants apply fixed 1st/99th-percentile cutoffs before standardization. All specifications use common samples across fixed-effect designs and standard errors clustered by firm and year. Holm pFYp_{FY} adjusts the three debt-share outcomes within each firm-effect ratio specification. The industry/year ETI models for bank and other-debt shares, and the firm/year untrimmed change/change model for other-debt share, required a positive-semidefinite repair; no other model displayed here did. For the bank-share ETI model, the standardized-coordinate result is p=.626p = .626; the native-coordinate and unrepaired alternatives are documented in Table A3, where the full range is .374.374–.627.627. These ratio estimates are checks on tail sensitivity, not preferred climate-information measures.

MeasureNNMissing (%)Zero (%)Negative (%)MeanSDP1MedianP99MinimumMaximum
Emissions-to-Talk Index13,41017.529.328.60.00300.0439−0.08330.00000.1149−1.13681.5409
Presentation-only emissions/talk ratio9,51941.529.629.2168.70301,604.4850−2,245.67870.00004,311.1770−8,117.302069,705.1100
Change in emissions/change in talk11,39429.929.335.3−3,606.8777382,359.4000−12,390.29170.000011,214.2303−40,242,212.00002,623,801.5000
Presentation talk frequency16,0401.329.00.00.0010470.0027140.0000000.0002610.0138500.0000000.046609

Table A1. Distribution of the ETI and alternative ratio measures. Notes: Missing shares use all 16,258 firm–years. Zero shares are calculated among nonmissing observations. The presentation-only and change/change rows summarize the additional ratio fields; they are not restricted to a regression sample. The former divides an emissions change by presentation talk, while the latter divides an emissions change by a change in presentation talk. The ETI is also shown, in its raw units. The extreme ratio distributions motivate reporting results across definitions and sample rules.

Low substitutabilityHigh concentrationFew competitors
Industry/yearFirm/yearIndustry/yearFirm/yearIndustry/yearFirm/year
ETI−0.17996 (0.08965) p=.073p = .073−0.05799 (0.07227) p=.441p = .441−0.18305 (0.07709) p=.039p = .039−0.03673 (0.06869) p=.605p = .605−0.20107 (0.07766) p=.027p = .027−0.05790 (0.06765) p=.412p = .412
Index × moderator0.30353 (0.14767) p=.067p = .0670.12041 (0.12225) p=.348p = .3480.33652 (0.09833) p=.007p = .0070.07375 (0.11174) p=.524p = .5240.41550 (0.11098) p=.004p = .0040.17021 (0.10121) p=.124p = .124
Moderator−0.04480 (0.01512) p=.014p = .014−0.05343 (0.01135) p=.001p = .001−0.00554 (0.00642) p=.409p = .4090.00738 (0.01252) p=.569p = .569−0.01682 (0.01806) p=.374p = .3740.00014 (0.01276) p=.991p = .991
Holm pp, interaction family.067.696.014.696.012.372
Observations10,69110,48310,69110,48310,69110,483
R2R^20.23460.78440.23420.78370.23450.7838

Table A7. Product-market competition: contemporaneous specification. Notes: The outcome is bank debt/total debt. These are contemporaneous specifications using the ETI. Moderators are lagged one year. All specifications include the full lagged control set and year effects; standard errors are clustered by firm and year. The Holm row adjusts the three interaction pp-values separately within each fixed-effect design. A four-firm concentration-ratio moderator is not included among these splits. These interactions describe heterogeneity and do not identify a channel.

Dividend payerHigh Altman Z-scoreHigh market capitalization
Industry/yearFirm/yearIndustry/yearFirm/yearIndustry/yearFirm/year
ETI−0.13125-0.13125−0.03553-0.03553−0.20482-0.20482−0.06511-0.06511−0.10522-0.10522−0.01212-0.01212
(0.05429)(0.05429)(0.05884)(0.05884)(0.09502)(0.09502)(0.05638)(0.05638)(0.03438)(0.03438)(0.04982)(0.04982)
p=.036p = .036p=.559p = .559p=.057p = .057p=.275p = .275p=.012p = .012p=.813p = .813
Index × moderator0.371670.371670.176560.176560.414060.414060.209060.209060.105750.10575−0.02282-0.02282
(0.23016)(0.23016)(0.14612)(0.14612)(0.23877)(0.23877)(0.10080)(0.10080)(0.11191)(0.11191)(0.08549)(0.08549)
p=.137p = .137p=.255p = .255p=.114p = .114p=.065p = .065p=.367p = .367p=.795p = .795
Moderator−0.02381-0.02381−0.00403-0.00403−0.02432-0.02432−0.02489-0.02489−0.06714-0.06714−0.02187-0.02187
(0.01564)(0.01564)(0.01529)(0.01529)(0.01611)(0.01611)(0.00896)(0.00896)(0.01980)(0.01980)(0.01205)(0.01205)
p=.159p = .159p=.797p = .797p=.162p = .162p=.020p = .020p=.007p = .007p=.100p = .100
Holm pp, interaction family.342.342.510.510.342.342.195.195.367.367.795.795
Observations10,69110,48310,69110,48310,69110,483
R2R^20.23470.78380.23490.78400.23750.7839

Table A8. Financial health: contemporaneous specification. Notes: Models and inference follow the contemporaneous specification in Table A7. The Holm row adjusts the three interaction pp-values separately within each fixed-effect design. The high-Z-score interaction has raw p=.065p = .065 with firm effects and Holm p=.195p = .195. A Whited–Wu-index interaction [37] is not included among these splits.

FamilyModerator at t−1t-1Industry + year FEFirm + year FENNFirmsYears
CompetitionLow substitutability0.00769 (0.01819) p=.682p = .682−0.00564 (0.01422) p=.701p = .7018,3341,56010
CompetitionHigh concentration0.00335 (0.01586) p=.838p = .838−0.00370 (0.01753) p=.837p = .8378,3341,56010
CompetitionFew competitors0.00544 (0.01937) p=.785p = .785−0.01078 (0.01728) p=.548p = .5488,3341,56010
Financial healthDividend payer0.02118 (0.01665) p=.235p = .2350.01638 (0.00760) p=.060p = .0608,3051,55810
Financial healthHigh Altman Z-score0.01195 (0.02318) p=.619p = .6190.00209 (0.01755) p=.908p = .9088,3341,56010
Financial healthHigh market capitalization−0.01309 (0.00944) p=.199p = .199−0.01425 (0.00604) p=.043p = .0438,3341,56010
OpacityHigh analyst dispersion−0.00059 (0.00822) p=.944p = .9440.01137 (0.00835) p=.206p = .2066,5681,26110
OpacityLow analyst coverage−0.00023 (0.00618) p=.971p = .9710.00014 (0.00575) p=.981p = .9816,8731,31610
OpacityHigh bid–ask proxy0.01537 (0.00856) p=.106p = .1060.01311 (0.00586) p=.052p = .0528,2761,55510
OpacityHigh intangibles0.02000 (0.00889) p=.051p = .0510.01293 (0.00284) p=.001p = .0018,2351,55410

Table A10. Exact-lag interaction checks

Notes: Entries are coefficients on the one-SD ETI × moderator term, followed by standard errors and raw pp-values. One-SD effects use the pooled exact-lag index standard deviation, 0.043628. The index, moderators and rebuilt controls are dated t−1t-1 by exact calendar year; the debt-share outcome is dated tt. Industry/year and firm/year models use the same observations within each row and standard errors are clustered by firm and year. Every industry/year covariance in this table required a positive-semidefinite repair. Among the firm/year models, only high analyst dispersion and high intangibles required it. Holm adjustment within each family leaves no competition interaction below .10. In the financial-health family, the firm-effect dividend and market-capitalization interactions each have adjusted p=.128p = .128. In the opacity family, the firm-effect intangibles interaction has adjusted p=.0055p = .0055; adjusting the two-way result across all ten interactions gives p=.0137p = .0137. That result is coordinate-sensitive. An exact null-imposed year-cluster check gives p=.043p = .043 before and .391 after Holm adjustment across all ten moderators. The interaction is therefore exploratory rather than a general mechanism result.

PanelPrior incident measureIndustry + year FEFirm + year FENIYN_{IY}NFYN_{FY}
Alog(1 + all ESG incidents)−0.03665 (0.00707) p=≤.001p = \leq.001−0.01037 (0.00476) p=.054p = .05410,69110,483
Alog(1 + greenwashing incidents)−0.02735 (0.01822) p=.164p = .1640.00066 (0.00864) p=.940p = .94010,69110,483
BEnvironmental incidents, standardized−0.02060 (0.00701) p=.015p = .015−0.00610 (0.00228) p=.023p = .02310,37310,373
BAny greenwashing incident0.01187 (0.01437) p=.428p = .428−0.00156 (0.00728) p=.835p = .83510,37310,373
BAll ESG incidents, standardized, standalone−0.03844 (0.00714) p=≤.001p = \leq.001−0.01128 (0.00475) p=.039p = .03910,37310,373
BEnvironmental incidents conditional on all incidents0.00976 (0.00788) p=.244p = .244−0.00156 (0.00253) p=.550p = .55010,37310,373

Table A12. Prior RepRisk incidents and bank debt share. Notes: Panel A uses logged-count specifications on each fixed-effect-specific sample. Panel B uses a common sample and distinguishes environmental incidents from a binary greenwashing indicator and total incident activity. Continuous Panel B measures are standardized. Models include the full lagged controls and two-way firm/year clustering. The environmental coefficient becomes small and insignificant when total incidents enter, while the greenwashing-specific coefficient is insignificant throughout. RepRisk records negative-news incidents; it is not another construction of the emissions-to-talk index.

Notes: Panel A reports the exact coefficient-stability calculation with the full coefficient targeted at zero. Short and full models use the same observations and fixed effects. The full model adds lagged emissions and six financial controls to the index-only short model, or adds the six financial controls to the index-plus-emissions short model. Rmax⁡R_{\max} is either min⁡(1,1.3RF2)\min(1,1.3R^{2}_{F}) or one. The large changes in δ\delta across short-model and Rmax⁡R_{\max} choices show that the calculation is not a stand-alone identification result. Panel B applies Frank’s published-results formula to the specification’s two-way-clustered tt-statistic. The original ITCV derivation is for conventional OLS inference, so the cluster-calibrated row is an analogue, not an exact extension to multiway clustered covariance.

Any linked facilityNumber of linked facilitiesLog linked facility amount
Industry/yearFirm/yearIndustry/yearFirm/yearIndustry/yearFirm/year
Emissions-to-Talk Index, standardized0.008**0.0000.017**0.0020.173**0.005
(0.003)(0.003)(0.007)(0.006)(0.062)(0.058)
Lagged log emissions0.057***−0.0000.109***0.0411.224***0.044
(0.010)(0.019)(0.020)(0.027)(0.209)(0.388)
Full lagged controlsYesYesYesYesYesYes
Observations10,91210,71410,91210,71410,91210,714
R2R^20.1270.4190.0930.4060.1340.432

Table A15. Firm–year DealScan outcomes and the Emissions-to-Talk Index. Notes: These estimates are taken from the corrected workbook; the full aggregation path was not independently rerun for this table. The workbook describes firm–year aggregates built from the one-record-per-facility file: an indicator for any linked facility, the number of linked facilities, and log linked facility amount. The Emissions-to-Talk Index is standardized, and each model includes lagged log emissions and the full lagged control set. Industry/year and firm/year models use fixed-effect-specific samples with two-way firm/year clustering. Appearance in the linked extract measures matched borrowing, not all bank borrowing; a non-match does not establish that the firm obtained no bank credit elsewhere. Ratio-free and RepRisk firm/year results appear in Table A28.

Information at t−1t - 1Any facilityLog facility countLog facility amountMean AISD spreadMean maturity
Talk ×\times emissions change0.0034<br>(0.0048)<br>p=.498p = .498−0.0007<br>(0.0047)<br>p=.878p = .8780.0563<br>(0.0979)<br>p=.583p = .583−2.1090<br>(1.2529)<br>p=.136p = .1360.5907<br>(0.3362)<br>p=.122p = .122
High talk, rising emissions0.0250<br>(0.0175)<br>p=.198p = .1980.0335<br>(0.0136)<br>p=.043p = .0430.5481<br>(0.3520)<br>p=.163p = .1631.3377<br>(4.8651)<br>p=.791p = .7910.7711<br>(0.8011)<br>p=.368p = .368
RepRisk environmental incidents0.0048<br>(0.0127)<br>p=.714p = .7140.0022<br>(0.0093)<br>p=.816p = .8160.0835<br>(0.2718)<br>p=.767p = .7670.3908<br>(1.9263)<br>p=.844p = .844−0.3566<br>(0.5173)<br>p=.510p = .510
Any RepRisk greenwashing incident−0.0092<br>(0.0276)<br>p=.747p = .7470.0048<br>(0.0341)<br>p=.892p = .892−0.1942<br>(0.6131)<br>p=.760p = .760−1.9342<br>(6.2773)<br>p=.766p = .766−1.5878<br>(1.7712)<br>p=.396p = .396

Table A28. Climate information and firm–year outcomes in the supplied DealScan extract

Notes: These estimates are taken from the corrected workbook and were not independently rerun for this table. The outcomes are the number of financial covenants, a secured indicator and log maturity on accepted facilities in the one-record-per-facility file. The Emissions-to-Talk Index is standardized, and each model includes log facility amount and the firm control set. Facilities with unknown security status are coded as unsecured, whereas the analyses in Table A27 leave them missing. Standard errors are clustered by firm. The displayed pp-values were calculated from the workbook tt-statistics using firm-cluster degrees of freedom and are shown to three decimals. Ratio-free and RepRisk contract results with firm/year clustering appear in Table A27.

Fixed effectsInformation at t−1t-1Log AISD spreadLog maturitySecuredCovenantsRevolver
Firm/yearTalk ×\times emissions change−0.0090 (0.0060) p=.176p = .1760.0214 (0.0058) p=.008p = .008−0.0046 (0.0038) p=.268p = .2680.0117 (0.0166) p=.504p = .504−0.0117 (0.0044) p=.032p = .032
Firm/yearHigh talk, rising emissions−0.0107 (0.0296) p=.729p = .7290.0202 (0.0426) p=.650p = .6500.0010 (0.0194) p=.962p = .962−0.0453 (0.0558) p=.444p = .444−0.0096 (0.0326) p=.777p = .777
Firm/yearRepRisk environmental incidents0.0114 (0.0124) p=.384p = .384−0.0022 (0.0209) p=.919p = .919−0.0082 (0.0107) p=.463p = .463−0.0335 (0.0263) p=.239p = .239−0.0028 (0.0120) p=.821p = .821
Firm/yearAny RepRisk greenwashing incident−0.0400 (0.0473) p=.422p = .422−0.0633 (0.0970) p=.532p = .532−0.0086 (0.0280) p=.766p = .766−0.0187 (0.0677) p=.789p = .7890.0266 (0.0355) p=.474p = .474
Industry/yearTalk ×\times emissions change−0.0042 (0.0063) p=.524p = .5240.0118 (0.0066) p=.120p = .120−0.0011 (0.0045) p=.811p = .8110.0105 (0.0166) p=.547p = .547−0.0009 (0.0088) p=.926p = .926
Industry/yearHigh talk, rising emissions−0.0363 (0.0395) p=.389p = .3890.0221 (0.0436) p=.627p = .6270.0950 (0.0385) p=.043p = .0430.1191 (0.0660) p=.114p = .114−0.0072 (0.0255) p=.786p = .786
Industry/yearRepRisk environmental incidents−0.0026 (0.0169) p=.883p = .883−0.0003 (0.0171) p=.987p = .9870.0154 (0.0201) p=.467p = .467−0.0316 (0.0317) p=.349p = .3490.0171 (0.0056) p=.015p = .015
Industry/yearAny RepRisk greenwashing incident−0.0326 (0.0617) p=.612p = .612−0.1505 (0.0549) p=.025p = .025−0.0711 (0.0459) p=.160p = .160−0.0862 (0.1215) p=.498p = .4980.0599 (0.0341) p=.117p = .117

Table A27. Ratio-free climate information and terms of accepted DealScan facilities

OutcomeInformation term at t−1t - 1Firm + year FEIndustry + year FEHolm pFYp_{FY}NNFirmsYears
Log total debtTalk ×\times emissions change0.00230.0023<br>(0.0049)(0.0049)<br>p=.651p = .6510.01040.0104<br>(0.0094)(0.0094)<br>p=.297p = .2971.0007,9621,49810
Total debt/assetsTalk ×\times emissions change−0.0001-0.0001<br>(0.0010)(0.0010)<br>p=.916p = .9160.00100.0010<br>(0.0014)(0.0014)<br>p=.500p = .5001.0008,3391,55810
Log total debtHigh talk, rising emissions0.03140.0314<br>(0.0222)(0.0222)<br>p=.190p = .1900.02360.0236<br>(0.0147)(0.0147)<br>p=.142p = .142.9907,9851,50110
Total debt/assetsHigh talk, rising emissions−0.0043-0.0043<br>(0.0059)(0.0059)<br>p=.486p = .486−0.0022-0.0022<br>(0.0035)(0.0035)<br>p=.536p = .5361.0008,3621,56110
Log total debtEnvironmental incidents0.00380.0038<br>(0.0095)(0.0095)<br>p=.696p = .6960.00670.0067<br>(0.0058)(0.0058)<br>p=.279p = .279.7389,9891,73911
Total debt/assetsEnvironmental incidents0.00470.0047<br>(0.0021)(0.0021)<br>p=.054p = .0540.00260.0026<br>(0.0011)(0.0011)<br>p=.043p = .043.21510,5871,83311
Log total debtAny greenwashing incident−0.0242-0.0242<br>(0.0258)(0.0258)<br>p=.369p = .369−0.0294-0.0294<br>(0.0334)(0.0334)<br>p=.400p = .400.7389,9891,73911
Total debt/assetsAny greenwashing incident−0.0078-0.0078<br>(0.0047)(0.0047)<br>p=.131p = .131−0.0070-0.0070<br>(0.0046)(0.0046)<br>p=.161p = .161.39310,5871,83311

Table A17. Ratio-free climate-information terms and total debt

Notes: Total debt/assets is rebuilt as (dltt + dlc)/assets; log total debt is defined when the sum is positive. Models include the lagged dependent variable, lagged emissions and the remaining lagged controls. Continuous information variables are standardized; the high-talk/rising and any-greenwashing indicators remain binary. Standard errors are clustered by firm and year. Holm pFYp_{FY} adjusts across both outcomes within each specification: six continuous coefficients, six quadrant indicators, or four RepRisk coefficients. The industry/year covariance required a positive-semidefinite repair for both outcomes in the continuous and quadrant specifications and for total debt/assets, but not log total debt, in the RepRisk specification; no displayed firm/year covariance required it. The table addresses changes in the total-debt denominator without imputing bank or bond dollar amounts from shares.

Added control or absorbed effectsIndustry-design estimateFirm-design estimateNIYN_{IY}NFYN_{FY}
Current LSEG ESG score−0.09288 (0.03884) p=.038p = .038−0.01508 (0.05037) p=.771p = .77110,69010,482
Current LSEG Emissions score−0.09409 (0.03718) p=.030p = .030−0.01721 (0.05163) p=.746p = .74610,68810,481
Lagged LSEG ESG score−0.09588 (0.03908) p=.034p = .034−0.01683 (0.05137) p=.750p = .75010,69110,483
Lagged LSEG Emissions score−0.09537 (0.03800) p=.031p = .031−0.01764 (0.05169) p=.740p = .74010,68710,480
Two-digit SIC × year effects−0.08750 (0.03088) p=.018p = .018−0.03342 (0.06043) p=.592p = .59210,63710,429

Table A18. Robustness of the ETI coefficient to added scores and absorbed effects

Notes: Estimates are for the ETI with the full lagged control set and firm/year clustering. “Industry design” means industry and year effects in the score rows and two-digit SIC-by-year effects in the final row. “Firm design” means firm and year effects in the score rows and firm plus two-digit-SIC-by-year effects in the final row. None of the firm-design coefficients is statistically distinguishable from zero.

Fixed-protocol coefficientYearsEstimateYear-CR1 ppWCR ppTwo-way ppHolm WCR pp
Talk ×\times emissions change →\to bank share10−0.0002.878.852.865.852
High talk/rising emissions →\to bank share100.0101.144.117.193.352
Environmental incidents →\to bank share11−0.0061.017.024.023.141
High talk/rising emissions →\to any greenwashing incident100.0139.038.045.061.180
Talk ×\times emissions change →\to DealScan log spread8−0.0090.188.242.176.484
High talk/rising emissions →\to DealScan facility count80.0335.027.023.043.141

Table A20. Exhaustively enumerated year-cluster wild-bootstrap checks

Notes: The models use firm and year effects and the samples and controls specified for each regression. Year-CR1 clusters by outcome year only. WCR is the null-imposed, restricted-residual wild-cluster bootstrap-tt with every distinct two-sided Rademacher year-sign assignment enumerated: 128 assignments for eight years, 512 for ten, and 1,024 for eleven. The two-way column reports the firm/year-clustered result. Holm values adjust the six WCR tests displayed here. Exhaustive enumeration removes simulation error but does not make the bootstrap finite-sample exact under arbitrary errors. Because WCR clusters only by year, it does not model within-firm dependence and does not replace two-way clustering.

Outcome at ttPrepared presentation at t−1t-1Answer section at t−1t-1Holm pp, preparedHolm pp, answer
Change in log emissions0.003753 (0.005314) p=.498p = .4980.002660 (0.002981) p=.395p = .3951.0001.000
LSEG Emissions score−0.072713 (0.143263) p=.623p = .6230.224794 (0.149393) p=.163p = .1631.0001.000
LSEG ESG score−0.055051 (0.105003) p=.612p = .6120.066700 (0.091792) p=.484p = .4841.0001.000
Any RepRisk greenwashing incident0.007502 (0.003259) p=.044p = .044−0.001904 (0.001949) p=.352p = .352.7501.000
log⁡(1+greenwashing incidents)\log(1 + \text{greenwashing incidents})0.009568 (0.002367) p=.002p = .002−0.001057 (0.002366) p=.665p = .665.0491.000
log⁡(1+environmental incidents)\log(1 + \text{environmental incidents})0.005220 (0.005661) p=.378p = .3780.010714 (0.002978) p=.005p = .0051.000.097
log⁡(1+misleading-communication incidents)\log(1 + \text{misleading-communication incidents})0.008396 (0.005213) p=.138p = .1380.001791 (0.004119) p=.673p = .6731.0001.000

Table A22. Exploratory checks by earnings-call segment

Notes: Each row is a joint firm/year-effects model containing standardized log-transformed presentation and answer frequencies, rebuilt lagged controls and the lagged dependent variable. Standard errors are clustered by firm and year. The row-specific sample sizes are 8,388 for emissions change; 10,508 for the Emissions score; 10,511 for the ESG score; and 10,512 for each incident outcome. These samples contain 1,565 and 1,827–1,828 firms, respectively. The last two columns are section-wide Holm adjustments over coefficient and joint tests. Results are associations about incremental segment content, not causal effects.

Outcome at ttConfiguration at t−1t-1Firm + year FEIndustry + year FEHolm pFYp_{FY}NN
Any greenwashing incidentHigh talk, rising emissions0.0139 (0.0065) p=.061p = .0610.0132 (0.0083) p=.146p = .146.5528,380
Any greenwashing incidentTalk ×\times emissions change0.0008 (0.0014) p=.567p = .5670.0004 (0.0014) p=.762p = .7621.0008,357
log⁡(1+environmental incidents)\log(1 + \text{environmental incidents})High talk, rising emissions−0.0005-0.0005 (0.0230) p=.985p = .9850.0654 (0.0300) p=.057p = .0571.0008,380
log⁡(1+environmental incidents)\log(1 + \text{environmental incidents})Talk ×\times emissions change0.0025 (0.0044) p=.579p = .5790.0035 (0.0064) p=.597p = .5971.0008,357
log⁡(1+greenwashing incidents)\log(1 + \text{greenwashing incidents})High talk, rising emissions0.0113 (0.0054) p=.066p = .0660.0150 (0.0084) p=.107p = .107.5528,380
log⁡(1+greenwashing incidents)\log(1 + \text{greenwashing incidents})Talk ×\times emissions change0.0011 (0.0011) p=.371p = .3710.0003 (0.0019) p=.895p = .8951.0008,357

Table A23. Ratio-free configurations and subsequent RepRisk incidents

Notes: These regressions examine whether the measures predict later RepRisk incidents. Continuous terms are scaled by one SD, and all regressors use exact calendar lags. The binary-outcome specification is a linear probability model. Standard errors are clustered by firm and year. Holm values use the nine firm-effect coefficients in the relevant continuous or configuration family (three terms or configurations across three outcomes).

(1)(2)(3)(4)(5)(6)(7)
(1) ETI1.000<br>[13,410]
(2) Log total emissions−0.029∗∗∗-0.029^{***}<br>[13,410]1.000<br>[16,258]
(3) TalkFreq−0.028∗∗∗-0.028^{***}<br>[13,410]0.204∗∗∗0.204^{***}<br>[16,258]1.000<br>[16,258]
(4) LSEG ESG score−0.041∗∗∗-0.041^{***}<br>[13,409]0.411∗∗∗0.411^{***}<br>[16,257]0.104∗∗∗0.104^{***}<br>[16,257]1.000<br>[16,257]
(5) LSEG Emissions score−0.049∗∗∗-0.049^{***}<br>[13,405]0.462∗∗∗0.462^{***}<br>[16,249]0.151∗∗∗0.151^{***}<br>[16,249]0.833∗∗∗0.833^{***}<br>[16,249]1.000<br>[16,249]
(6) Firm size−0.037∗∗∗-0.037^{***}<br>[13,409]0.529∗∗∗0.529^{***}<br>[16,257]0.097∗∗∗0.097^{***}<br>[16,257]0.567∗∗∗0.567^{***}<br>[16,256]0.582∗∗∗0.582^{***}<br>[16,248]1.000<br>[16,257]
(7) Bank debt share0.004<br>[13,182]−0.272∗∗∗-0.272^{***}<br>[15,912]−0.070∗∗∗-0.070^{***}<br>[15,912]−0.265∗∗∗-0.265^{***}<br>[15,911]−0.279∗∗∗-0.279^{***}<br>[15,903]−0.351∗∗∗-0.351^{***}<br>[15,911]1.000<br>[15,912]

Table A25. Table A25: Pairwise Pearson correlations: ETI and principal variables. Notes: Pairwise-complete observation counts appear in brackets. The ETI is the emissions-growth-to-prior-talk ratio. TalkFreq combines the presentation and management-answer portions and is scaled by ten; scaling does not affect correlations. Variables are contemporaneous firm-year observations, although the ETI formula embeds prior talk. Stars denote two-sided p<.10p < .10, p<.05p < .05 and p<.01p < .01.

PanelTermFixed effectsEffect (pp)95% CI (pp)Raw ppHolm ppNN
AIncidents at t−2t-2Industry/year−0.1209-0.1209[−1.732,1.490]\left[-1.732, 1.490\right].8671.0006,526
AIncidents at t−1t-1Industry/year−0.5948-0.5948[−2.468,1.278]\left[-2.468, 1.278\right].4851.0006,526
AIncidents at ttIndustry/year−0.0174-0.0174[−2.047,2.012]\left[-2.047, 2.012\right].9851.0006,526
AIncidents at t+1t+1Industry/year−1.0963-1.0963[−2.786,0.593]\left[-2.786, 0.593\right].173.6926,526
AIncidents at t−2t-2Firm/year−0.0567-0.0567[−1.234,1.120]\left[-1.234, 1.120\right].9141.0006,526
AIncidents at t−1t-1Firm/year−0.4169-0.4169[−1.151,0.317]\left[-1.151, 0.317\right].227.9066,526
AIncidents at ttFirm/year0.13010.1301[−0.856,1.116]\left[-0.856, 1.116\right].7691.0006,526
AIncidents at t+1t+1Firm/year−0.6234-0.6234[−2.009,0.762]\left[-2.009, 0.762\right].330.9906,526
BEvent time ≤−3\leq-3Industry/year−10.9535-10.9535[−17.386,−4.521]\left[-17.386, -4.521\right].004.0117,636
BEvent time −2-2Industry/year−6.6437-6.6437[−12.831,−0.457]\left[-12.831, -0.457\right].038.0387,636
BFirst incident yearIndustry/year−10.2812-10.2812[−17.242,−3.320]\left[-17.242, -3.320\right].008.0167,636
BEvent time +1+1Industry/year−12.3126-12.3126[−16.965,−7.660]\left[-16.965, -7.660\right]<.001<.001<.001<.0017,636
BEvent time +2+2Industry/year−14.6099-14.6099[−20.312,−8.908]\left[-20.312, -8.908\right]<.001<.001<.001<.0017,636
BEvent time ≥+3\geq+3Industry/year−14.1559-14.1559[−19.429,−8.883]\left[-19.429, -8.883\right]<.001<.001<.001<.0017,636
BEvent time ≤−3\leq-3Firm/year−2.6496-2.6496[−7.553,2.253]\left[-7.553, 2.253\right].2561.0007,636
BEvent time −2-2Firm/year0.93700.9370[−1.102,2.975]\left[-1.102, 2.975\right].3301.0007,636
BFirst incident yearFirm/year−0.4105-0.4105[−2.193,1.372]\left[-2.193, 1.372\right].6191.0007,636
BEvent time +1+1Firm/year−0.5500-0.5500[−2.941,1.841]\left[-2.941, 1.841\right].6191.0007,636
BEvent time +2+2Firm/year−3.0002-3.0002[−6.751,0.751]\left[-6.751, 0.751\right].105.6307,636
BEvent time ≥+3\geq+3Firm/year1.25661.2566[−3.452,5.965]\left[-3.452, 5.965\right].5651.0007,636

Table A26. RepRisk environmental incidents and bank debt share over time

Notes: Panel A jointly includes the four displayed standardized incident terms and has nine year clusters. Panel B includes never-treated firms and firms whose first positive environmental incident appears in 2012–2019 after two observed zero-incident years; event time −1-1 is omitted and there are eleven year clusters. It is a descriptive two-way-fixed-effect event-time check, not a staggered-adoption causal design. Standard errors are clustered by firm and year. Both Panel B covariance matrices, for the industry/year and firm/year models, required a positive-semidefinite repair; neither Panel A covariance did. The industry-effect pre-event differences and the firm-effect joint pre-event test (p=.039p=.039) caution against a causal reading.

Notes: The unique-facility file is restricted to complete years 2010–2019. Ratio-free models use 2012–2019 (eight year clusters); RepRisk models use 2011–2019 (nine). For log spread, interaction, configuration and RepRisk samples are 1,946/425 firms, 1,950/427 and 2,486/524. For the other outcomes they are 2,166/459, 2,172/460 and 2,755/560. Each industry/year row uses the same observations as its firm/year counterpart. Unknown security status is missing rather than coded as unsecured; this affects 5,518 facilities in the full file. Standard errors are clustered by firm and year. Recorded covariance repairs apply to: industry/year spread in both ratio-free specifications; maturity in both fixed-effect designs for both ratio-free specifications and in the firm/year RepRisk model; secured status in both fixed-effect designs for the continuous specification and in the firm/year quadrant model; firm/year covenants and revolver in the continuous specification; industry/year covenants and revolver in the quadrant specification; and industry/year revolver in the RepRisk specification. Each RepRisk model contains both displayed incident terms. No other model displayed here required repair. Within each fixed-effect design, the Holm families contain 15 continuous, 15 quadrant and 10 RepRisk tests. The smallest within-specification Holm pp is .115 and every global-primary Holm value equals one.

Notes: Firm and year effects and exact-lag controls are included. The first three outcomes measure appearance or volume in the supplied extract; a zero does not establish that the firm obtained no bank loan elsewhere. Interaction/configuration samples are 6,572/6,596 observations for the first three outcomes, 1,639/1,642 for mean spread and 1,913/1,918 for mean maturity. RepRisk samples are 8,645, 2,170 and 2,508, respectively. Standard errors are clustered by firm and year. Recorded covariance repairs apply to mean spread in all three information specifications and, in the quadrant specification, to log facility count and log facility amount. Each RepRisk model contains both displayed incident terms. No other displayed model required repair. The Holm families contain 15 continuous, 15 quadrant and 10 RepRisk tests. The smallest specification-level Holm value is .646.

SampleOutcomeInformation at t−1t - 1Firm/year estimateHolm ppNNYear clusters
All currenciesLog spreadTalk × emissions change−0.0104 (0.0053); p=.087p = .0871.0001,9468
All currenciesLog spreadHigh talk, rising emissions−0.0113 (0.0290); p=.707p = .7071.0001,9508
All currenciesLog spreadRepRisk environmental incidents0.0085 (0.0155); p=.598p = .5981.0002,4869
All currenciesLog spreadAny RepRisk greenwashing incident−0.0091 (0.0506); p=.861p = .8611.0002,4869
All currenciesSecuredTalk × emissions change−0.0040 (0.0035); p=.294p = .2941.0002,1668
All currenciesSecuredHigh talk, rising emissions0.0012 (0.0205); p=.957p = .9571.0002,1728
All currenciesSecuredRepRisk environmental incidents−0.0092 (0.0110); p=.425p = .4251.0002,7559
All currenciesSecuredAny RepRisk greenwashing incident−0.0150 (0.0249); p=.564p = .5641.0002,7559
USD onlyLog spreadTalk × emissions change−0.0109 (0.0052); p=.075p = .0751.0001,8548
USD onlyLog spreadHigh talk, rising emissions−0.0015 (0.0265); p=.955p = .9551.0001,8588
USD onlyLog spreadRepRisk environmental incidents0.0124 (0.0149); p=.429p = .4291.0002,3669
USD onlyLog spreadAny RepRisk greenwashing incident0.0081 (0.0501); p=.875p = .8751.0002,3669
USD onlySecuredTalk × emissions change−0.0041 (0.0037); p=.303p = .3031.0002,0338
USD onlySecuredHigh talk, rising emissions0.0023 (0.0186); p=.907p = .9071.0002,0398
USD onlySecuredRepRisk environmental incidents−0.0083 (0.0115); p=.492p = .4921.0002,5889
USD onlySecuredAny RepRisk greenwashing incident−0.0172 (0.0258); p=.523p = .5231.0002,5889

Table A29. Table A29: DealScan contract-composition and USD-only checks. Notes: All-currency models add grouped loan-type, deal-purpose and currency indicators; USD-only models add grouped type and purpose indicators. Groups with fewer than 20 facilities are pooled. Controls and complete-year restrictions match Table A27; unknown security status is missing rather than coded as unsecured. Each of the 12 firm/year models represented here (two samples × two outcomes × three information specifications) required a positive-semidefinite repair. All Holm-adjusted values equal one.

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