Maturity Matching in Unlisted Firms: The Within-Firm Evidence

1. Introduction

Research on small-firm debt has organised itself around two quantities. One is how much debt a firm carries, the other is what that debt costs. Both have been evaluated for Italian small firms with regression-discontinuity, survival and eligibility-threshold designs of a quality rarely achieved on administrative accounting data (Boschi, Girardi & Ventura, 2014; de Blasio et al., 2018; D’Ignazio & Menon, 2020; Lagazio, Persico & Querci, 2021). A third quantity sits in every filed balance sheet, is available for essentially every firm-year, and is almost never treated as an outcome: how the debt stock is distributed across maturities. It is orthogonal to the level by construction, since the same leverage is compatible with any mix of short and long claims, and orthogonal to the price by observation, since the same lender quotes different rates for the same borrower at different horizons.

This paper asks what determines that composition in a population of firms that cannot issue bonds, and takes as its focal regressor the variable the theory of maturity choice makes central: the share of the balance sheet held in fixed assets. The prediction is old and unambiguous: a firm finances long-lived assets with long-lived claims, either because refinancing a long asset at a date it does not choose is imprudent, or because fixed assets are what a bank will lend against for a decade. What is missing is not the theory but the evidence, and the gap has three components.

The first is population. Körner (2007), Cai, Fairchild and Guney (2008), Alcock, Finn and Tan (2012), Etudaiye-Muhtar, Ahmad and Matemilola (2017), Kalsie and Nagpal (2018), Vijayakumaran and Vijayakumaran (2019) and Phan (2020) span four continents and two decades, and are composed almost entirely of exchange-listed firms whose access to bond markets and rating agencies makes maturity a genuinely open choice. The refinements that followed—dispersion rather than average maturity, the profile rather than the level, the secular drift towards shorter debt (Gopalan, Song & Yerramilli, 2014; Choi, Hackbarth & Zechner, 2018; Byun, Lin & Wei, 2021; Clark & Park, 2023)—were made on the same population. The small-firm branch is thinner and reports the cross-sectional comparison as though it settled the within-firm one (Heyman, Deloof & Ooghe, 2008; Lopez-Gracia & Mestre-Barberá, 2015; Díaz-Díaz, García-Teruel & Martínez-Solano, 2016; D’Amato, 2020).

The second is the status of the regressor. Tangibility appears in the control vector of virtually every specification cited above, is consistently signed, and is virtually never the coefficient the paper is about. It is estimated hundreds of times without being interrogated once: rarely instrumented, rarely decomposed into its between and within parts, rarely tested for functional form, rarely measured twice.

The third is the outcome the collateral literature chooses. Work on pledgeability has moved quickly—enforcement costs and asset structure (Gopalan, Mukherjee & Singh, 2016), intangibles as collateral (Lim, Macias & Moeller, 2020), patent-pledging reforms (Dai et al., 2024; Chen et al., 2026; Wang, 2026)—but it asks whether a firm can borrow, how much and at what price. The horizon of the credit obtained is where the collateral mechanism should bite hardest, and it is left unexamined; Nakatani (2023) is among the few exceptions.

The setting allows a question that cannot be asked elsewhere. Innovative start-ups, innovative SMEs and ordinary SMEs are extracted from one source on identical items, so 73,662 firm-years on 11,265 firms over 2016–2024 can be compared across regimes without differential disclosure confounding the comparison. Three findings follow. Maturity matching is real inside firms and not only across them: the between coefficient is −0.380, the within coefficient −0.247. Adjustment is incomplete, with persistence bounded between 0.317 and 0.721 and a long-run response 1.8 times the static one. And the relationship is steeply graded by regime, from −0.312 among ordinary SMEs to −0.120 among innovative start-ups.

The design is what makes the third finding credible. A taxonomy estimated on nine accounting dimensions, with the regulatory register withheld entirely, reproduces the same gradient—evidence that certification selects balance sheets of a particular shape rather than creating it. Six flexible learners fitted to exactly the variation the fixed-effects estimator uses then improve on the linear form by a factor of 1.27, against the multiples of three to five such comparisons return on levels. The linear specification is shown adequate rather than assumed adequate—a claim panel papers ordinarily cannot make.

The article continues as follows. Section 2 reviews the literature on debt maturity, collateral and small-firm financing, and identifies the three gaps this study addresses. Section 3 describes the data and explains why three methods are used rather than one. Section 4 estimates the relationship across seven panel estimators and reports the dynamic and instrumented specifications. Section 5 partitions the same firms into a taxonomy of balance-sheet configurations and asks whether the coefficient of Section 4 describes one relationship or an average of several. Section 6 fits six flexible learners to the variation the fixed-effects estimator uses, to establish whether the linear form is adequate. Sections 7 to 10 discuss the results, draw the policy implications, state the limitations and conclude. Appendices A to C support the panel module, D to H the clustering exercise, and I to K the machine-learning validation.

2. Literature Review

What the maturity literature has established, and on whom. The modern treatment of debt maturity descends from two arguments made within a decade of each other. In the first, a firm that finances a long-lived asset with a short-lived claim exposes itself to refinancing at a date it does not choose, so the prudent policy is to match the maturity of liabilities to the maturity of assets. In the second, maturity is an instrument of governance: short debt disciplines managers by forcing them back to the credit market, and lenders shorten it precisely when they most doubt the borrower. Almost every empirical paper since has tested one of these two mechanisms, and the accumulated cross-sectional evidence is remarkably consistent in sign. Larger firms, more tangible firms and firms with better credit quality hold longer debt; growth options, information asymmetry and volatility shorten it. What the literature is far less consistent about is where that evidence comes from. Körner (2007) studies Czech firms, Cai, Fairchild and Guney (2008) Chinese ones, Alcock, Finn and Tan (2012) Australian ones, Etudaiye-Muhtar, Ahmad and Matemilola (2017) a panel of African countries, Kalsie and Nagpal (2018) NSE-listed Indian corporates, Vijayakumaran and Vijayakumaran (2019) Chinese listed companies, Phan (2020) listed Vietnamese enterprises, and Hussain, Shamsudin, Salehuddin and Jabarullah (2018) Malaysian shari’ah-compliant issuers. The list is long, geographically wide, and almost entirely composed of exchange-listed firms. Gopalan, Song and Yerramilli (2014), Choi, Hackbarth and Zechner (2018), Byun, Lin and Wei (2021) and Clark and Park (2023) refine the object of study—dispersion of maturities, the profile rather than the average, the secular drift towards shorter debt—but they refine it on the same population, whose access to bond markets, rating agencies and public equity makes the maturity decision a genuinely open choice. A second regularity concerns how tangibility enters. In this literature it is a control. It appears in the regressor vector of virtually every specification cited above, it is almost always signed negatively against the short-term share, and it is almost never the coefficient the paper is about. The consequence is that its magnitude is reported without being interrogated: rarely instrumented, rarely decomposed into its between and within components, rarely tested for functional form, and rarely measured in more than one way. A parameter that is estimated hundreds of times as a nuisance is not the same thing as a parameter that has been established.

Small firms, where the choice is narrower. The small-firm branch is more directly relevant and much thinner. Heyman, Deloof and Ooghe (2008) established for privately held Belgian firms that the determinants of financial structure differ from the listed benchmark; Lopez-Gracia and Mestre-Barberá (2015) show that agency conflicts operate on SME maturity through different channels than in large firms; Díaz-Díaz, García-Teruel and Martínez-Solano (2016) find that family control shifts maturity in Spanish private firms; Briozzo, Cardone-Riportella and García-Olalla (2019) and Dasilas (2024) trace governance attributes and credit ratings into the maturity and structure of non-listed SME debt. D’Amato (2020) is the closest antecedent to the present study, examining capital structure and debt maturity for SMEs across a financial crisis. More recently Gama and Vieira (2024) and Gama, Sol Murta and Vieira (2024) link conservative financing policies to societal trust and to the density of local bank branches, and Paeleman, Mataigne and Vanacker (2025) show that maturity structure, and not the debt level, predicts export withdrawal in international new ventures. Three limitations recur across this branch. Samples are small—typically a few thousand firm-years drawn from one country and a handful of years. Identification is cross-sectional or relies on short panels in which the within dimension is too thin to exploit, so the reported coefficient conflates the comparison between firms with the comparison of a firm against itself. And the dependent variable is usually a level of leverage with maturity treated as a secondary outcome, rather than the maturity composition treated as the object.

Collateral studied as access, not as horizon. The pledgeability literature has moved quickly and in a direction that makes the omission conspicuous. Gopalan, Mukherjee and Singh (2016) show that the cost of enforcing debt contracts shapes both financing and asset structure jointly. Lim, Macias and Moeller (2020) document that intangible assets support more debt than the collateral view predicts. Dai, Du, Gao, Gu and Wang (2024) and Wang (2026) exploit patent-pledging regimes in China to identify the effect of making a specific asset class collateralisable, and Chen, Pan, Qian, Wu and Xia (2026) push the same logic into innovation outcomes. Yang, Ma, Mi, Li and Chen (2026) go further still, treating collateral flexibility as an instrument for resolving maturity mismatch in supply-chain finance. The gap is precise. This literature asks whether a firm can borrow, how much, and at what price, and it establishes convincingly that pledgeable assets relax those margins. It rarely asks what happens to the horizon of the credit obtained. Yet the horizon is where the collateral mechanism should bite hardest: a bank will extend a five-year secured facility against a machine and a ninety-day revolving line against a receivable, so an asset-composition shock should show up in the maturity mix before it shows up in the leverage ratio. Nakatani (2023) is one of the few papers to connect the two explicitly, finding that debt maturity and productivity interact through the intangible share, and Deng and Liu (2024) and McGrattan (2020) supply the measurement apparatus for intangible capital that such work requires. Cortez (2025) surveys the emerging role of intangibles in capital-structure determination and reaches the same conclusion about what has not been done.

Maturity as regressor rather than outcome. A large body of work uses maturity as an explanatory variable. Dang (2011) and Kashefi Pour and Khansalar (2015) examine how leverage and maturity jointly govern investment and the underinvestment problem; Cutillas Gomariz and Sánchez Ballesta (2014) show that short maturity substitutes for reporting quality in disciplining investment; Khaw and Lee (2016), Wang, Wang and Xu (2022) and Nouman et al. (2023) trace maturity into investment efficiency and firm value under financial constraints; Petcharat and Mula (2026) and Li, Ye and Luo (2026) extend the design to ESG disclosure and earnings-forecast quality. On the risk side, Della Seta, Morellec and Zucchi (2020) model the risk-taking incentives created by short debt, Friewald, Nagler and Wagner (2022) price refinancing exposure in equity returns, He, Lütkebohmert and Xiao (2017) and Chaturvedi and Singh (2024) formalise rollover risk, and Huberman and Repullo (2025) return to the moral-hazard foundations. Wang, Chiu and King (2020), Chiu, King and Wang (2021) and Chu and Kjenstad (2023) establish that maturity and its dispersion are priced in loan spreads. Taken together this work makes the case that maturity composition matters for real and financial outcomes. It thereby raises, without answering, the question of what determines it in the population where the consequences are largest. It also proceeds almost universally from a static specification, imposing that maturity structure adjusts fully within the accounting year—an assumption that the persistence estimates reported in this paper reject.

Innovative firms and the Italian institutional setting. Two further literatures bear on the heterogeneity this study documents. The first concerns firms whose assets are largely uncollateralisable. Magri (2014) shows that equity issuance, not debt, supports R&D in unlisted Italian high-tech manufacturers; Hoffmann and Kleimeier (2021) price disclosure quality into innovative firms’ cost of debt; Castaldo, De Luca and Barile (2021) find that initial bank access predicts start-up default in Italy; Lee and Jung (2024), Liu and Chen (2023), Pisicoli, Marchionne and Beccari (2025) and Cattafi, Del Pozzo and Naciti (2025) examine the instruments—R&D human capital, banking deregulation, minibonds, green-innovation signalling—through which such firms obtain external finance. Haro-de-Rosario, Caba-Pérez and Cazorla-Papis (2016), Croce, Quas and Tenca (2025) and Runach, Garg and Narwal (2024) cover the venture-capital and bond alternatives. The second concerns the Italian bank–firm relationship and its public guarantee architecture, which has been evaluated with unusual rigour. Bartoli, Ferri, Murro and Rotondi (2013) and Gai, Ielasi and Rossolini (2016) study mutual guarantee institutions; Boschi, Girardi and Ventura (2014), de Blasio, De Mitri, D’Ignazio, Finaldi Russo and Stoppani (2018), D’Ignazio and Menon (2020), Caselli, Corbetta, Rossolini and Vecchi (2019), Caselli, Corbetta, Cucinelli and Rossolini (2021) and Lagazio, Persico and Querci (2021) evaluate the public schemes with regression-discontinuity, survival and eligibility-threshold designs; Corredera-Catalán, di Pietro and Trujillo-Ponce (2021) extend the comparison to Spain. Minetti, Murro, Rotondi and Zhu (2019), Fernández-Méndez and González (2019), Cerasi, Fedele and Miniaci (2017), Butzbach and Sarno (2019) and Falavigna, Ippoliti and Ramello (2026) document how local banking, ownership and judicial conditions shape credit terms.

These evaluations measure access, volume, cost and survival. None of them measures the horizon of the credit the guarantee delivers, which is the margin on which a scheme oriented towards short-term working-capital facilities would be expected to leave its clearest trace.

Method: taxonomies and validation. Finally, two methodological literatures are used rather than extended. João, Schaumburg, Lucas and Schwaab (2024) provide the reference treatment of nonparametric clustering on multivariate panel data; Gan and Valdez (2020) survey clustering in an actuarial-financial setting; Mikrou and Sapidis (2025) and Tran, Chang and Yu (2026) address the selection of algorithms and the role of validity indices; Viswanathan, Gopinathan and Rengasamy (2026) apply fuzzy clustering with membership diagnostics to bank ratings; Pongvijan and Trakunphutthirak (2026) argue for multi-metric rather than single-index evaluation; Xiang (2025) illustrates the single-algorithm, single-index practice that remains common in applied finance. On the regression side, Sinha and Vodwal (2023), Neves, Serrasqueiro, Dias and Hermano (2020), Haron et al. (2021), Canofari, Cucculelli, Piergallini and Renghini (2025), Iwaki (2019), Yuan (2026) and Paseda, Ashade, Manasseh and Olurin (2026) supply the panel and system-GMM practice this study follows. The common weakness is that flexible learners enter applied finance almost exclusively as predictors. They are rarely turned back on the econometric model to ask whether its functional form is adequate—which is the use made of them here.

The gap this study occupies. Placing the six strands side by side identifies a specific vacancy rather than a general one. The maturity literature has a well-developed theory, a stable set of cross-sectional findings and almost no evidence from firms that cannot issue bonds. The small-firm literature has the right population but reports the between comparison as though it were the within one. The collateral literature has the right regressor and the wrong outcome, having established what pledgeable assets do to the availability and price of credit while leaving its horizon unexamined. The investment literature treats maturity as given. The innovation-finance and guarantee literatures describe exactly the institutional environment in which the certified Italian populations operate, and measure every margin of credit except its term. And the methodological literatures supply tools—panel taxonomies, validity-index ensembles, flexible learners—that applied finance uses for description and prediction rather than for testing the specification it has already estimated. What follows occupies that vacancy on four fronts. It makes debt-maturity composition the dependent variable in a population of 11,265 unlisted Italian firms observed for up to nine years, of which two-fifths are certified innovative start-ups or innovative SMEs and the remainder ordinary SMEs extracted from the same source on identical items. It makes asset tangibility the focal regressor rather than a control, and measures both focal variables twice by independent routes through the balance sheet before estimating anything. It separates the between from the within comparison and reports both, then bounds the speed of adjustment that the static specification suppresses. And it subjects the resulting linear equation to two disciplines it did not choose: a taxonomy of balance-sheet configurations estimated without reference to the equation or to the regulatory register, and a battery of flexible learners fitted to exactly the variation the fixed-effects estimator uses. Neither discipline is decorative. The first shows that the regime heterogeneity is recoverable from accounts alone, which weakens the reading that certification itself produces it. The second shows that the flexible learners improve on the linear fit by a factor of 1.27 rather than the multiples of three to five that the same procedures return on levels—evidence that the functional form imposed in the panel module is adequate rather than convenient. See Table 1.

3. Data and Methodology

The data come from three extractions of AIDA (Bureau van Dijk), which harmonises the filed accounts of Italian limited companies. Innovative start-ups and innovative SMEs are drawn from the two special sections of the Business Register; ordinary SMEs from a comparison extraction of non-certified firms. All three share an identical variable structure, so every item is available for every group—the condition that makes a three-regime comparison meaningful rather than an artefact of differing disclosure. The estimation sample is 73,662 firm-year observations on 11,265 firms over 2016–2024: 2,213 innovative start-ups, 2,763 innovative SMEs and 6,289 ordinary SMEs. Continuous variables are winsorised at the first and ninety-ninth percentiles within year, and standard errors are clustered at firm level throughout.

The dependent variable is the short-term share of total debt, filed for 99.3 per cent of accounts. Tangibility is fixed assets over total assets, recovered exactly from the structural margin. Both are constructed twice by independent balance-sheet routes and the versions correlate at 0.984 and 0.666—a check the maturity literature does not ordinarily perform, and one that matters here because the sign instability reported across studies of private firms (Heyman, Deloof & Ooghe, 2008; D’Amato, 2020) is plausibly a measurement problem as much as an economic one.

Each module answers a question the others cannot, and the design is sequential rather than parallel.

The panel module estimates the coefficient. Pooled OLS, between, random effects, fixed effects, two-way fixed effects and two weighted variants are reported side by side because the between–within comparison is the diagnostic the SME literature omits: cross-sectional studies of private firms (Díaz-Díaz, García-Teruel & Martínez-Solano, 2016; Briozzo, Cardone-Riportella & García-Olalla, 2019) report the first and imply the second. A dynamic specification follows the bounding logic standard in this literature (Sinha & Vodwal, 2023; Neves, Serrasqueiro, Dias & Hermano, 2020), because the static form imposes full within-year adjustment. Instrumental variables address the simultaneity that the pledgeability literature identifies through policy shocks (Dai, Du, Gao, Gu & Wang, 2024; Wang, 2026) and which is unavailable here.

The clustering module asks whether one coefficient describes one relationship. A sample split chosen by the researcher inherits the hypothesis it tests; a taxonomy estimated on nine balance-sheet dimensions with the regulatory register withheld does not. Six algorithm families are compared on eleven validity indices with rank aggregation, following the multi-metric argument of Pongvijan and Trakunphutthirak (2026) and Mikrou and Sapidis (2025) against the single-index practice still common in applied finance, and drawing on panel-clustering (João, Schaumburg, Lucas & Schwaab, 2024) and financial-clustering (Gan & Valdez, 2020; Viswanathan, Gopinathan & Rengasamy, 2026) precedents.

The machine-learning module asks whether the functional form holds. Six learners are fitted to the same equation under three transformations—levels, Mundlak and firm- and year-demeaned—so that the comparison is against the variation the fixed-effects estimator actually uses. Cross-validation is grouped by firm. The purpose is validation, not prediction.

The structure is therefore cumulative: the first module produces a number, the second tests whether it is an average of heterogeneous relationships, the third tests whether the form that produced it is adequate. See Figure 1.

4. Debt Maturity and Asset Tangibility

Almost everything written about small-firm debt concerns two quantities: how much of it there is, and what it costs. A third quantity is measured in every filed account and is almost never used as an outcome—the composition of the debt stock across maturities. It is orthogonal to the level by construction, since a firm can hold the same leverage with any mix of short and long claims, and orthogonal to the price, since the same lender charges different rates for the same borrower at different horizons. This section asks what determines that composition, and takes as the focal regressor the variable the theory of maturity choice makes central and the empirical literature on Italian small firms has left almost untouched: the share of the balance sheet held in fixed assets.

The prediction is old and unambiguous. Under the matching principle of Myers (1977) and Hart and Moore (1994), a firm finances long-lived assets with long-lived claims, because a short claim against a long asset forces refinancing at a moment the borrower does not choose. Under the collateral reading of Barclay and Smith (1995), the same correlation arises for a different reason: fixed assets are what a bank will lend against for ten years, and a firm without them cannot obtain a ten-year loan whether or not it wants one. The two mechanisms are observationally close and this design does not separate them; what it does establish is whether the association survives the removal of firm heterogeneity, which is where most of the cross-sectional evidence has never been taken. See Table 2.

Neither variable required reconstruction and neither is shared with any dependent variable used elsewhere in this project. The maturity index is filed for 99.3 per cent of accounts, and fixed assets follow exactly from the structural margin, which is net worth minus fixed assets by definition. Both constructions were checked against an independent second route through the financial coverage ratio and the amortisation mix; the two versions of the dependent variable correlate at 0.984, and Appendix A reports the comparison. The distributions are described in Appendix A as well, and one feature of them matters for reading what follows: 31.3 per cent of firm-years hold no long-term debt at all, so the dependent variable piles up at its upper bound.

The first question is which estimator the data impose, and the answer is unambiguous in all three directions. The F test on joint significance of the individual effects is 9.31 and rejects; the Breusch–Pagan multiplier is 65,218.6; the Hausman statistic on four degrees of freedom is 313.96. Pooled OLS and random effects are both rejected, and two-way fixed effects is the reference specification. See Table 3.

The table reports one column per estimator; the figure places all seven on a common axis, so the distance between the cross-sectional and the within-firm readings of the same coefficient becomes visible. See Figure 2.

The coefficient is negative under every estimator and never comes close to zero. What Figure 1 makes visible is the size of the gap between the two extremes of the variance decomposition. Across firms the slope is −0.380: a firm holding ten percentage points more of its assets in fixed form finances 3.8 percentage points less of its debt at short maturity. Within firms it is −0.247. Roughly two-thirds of the cross-sectional gradient is reproduced when the firm is compared only with itself, which is a strong result by the standards of a literature that has almost always reported the first number and left the second unexamined. The remaining third is composition: firms that are permanently asset-heavy differ from firms that are permanently asset-light in ways the equation does not contain, and part of the raw correlation belongs to those differences rather than to the balance-sheet mechanism.

Scaled to the variation the fixed-effects estimator actually uses, the within coefficient implies that a one-standard-deviation increase in tangibility inside a firm—9.6 percentage points—shifts 2.3 percentage points of the debt stock out of short maturity, which is 18.9 per cent of a within-firm standard deviation of the dependent variable. That is a moderate effect, not a dominant one, and the honest statement is that asset composition moves maturity composition materially without determining it.

One objection to everything above is that the dependent variable is a proportion. It is bounded at zero and one, 31.3 per cent of firm-years sit exactly at the upper bound, and a linear model fitted to such a variable can in principle predict outside the admissible range and can misstate marginal effects near the boundary. The specification is therefore re-estimated as a fractional response model in the manner of Papke and Wooldridge, with a probit link, quasi-maximum likelihood, and a Mundlak correction that adds the firm mean of every time-varying regressor so that the estimator remains consistent under correlation between the effects and the covariates. Year effects and firm-clustered standard errors are retained. The joint test on the four firm means is decisive, χ²(4) = 609.2, which confirms that the correlated random-effects specification is required rather than optional and reproduces the ssmessage of the Hausman test in the linear setting.

Table 4. Fractional response estimates with Mundlak correction.

	Index coefficient	Average partial effect	z	Linear benchmark
TANG	−0.8425*** (0.0332)	−0.2144*** (0.0084)	−25.39	−0.2410*** (0.0102)
SIZE	−0.1683*** (0.0095)	−0.0428*** (0.0024)	−17.71	−0.0437*** (0.0025)
COVER	0.0255*** (0.0015)	0.0065*** (0.0004)	16.69	0.0069*** (0.0004)
GROWTH	0.0406*** (0.0052)	0.0103*** (0.0013)	7.78	0.0103*** (0.0015)
Mundlak test, χ²(4)	609.2***
Observations	73,662
Firms	11,265

Note. Dependent variable: short-term debt over total debt. Fractional probit estimated by quasi-maximum likelihood with the firm mean of each time-varying regressor added as a Mundlak correction, year effects, and standard errors clustered at firm level, reported in parentheses. *** p < 0.01, ** p < 0.05, * p < 0.10. Average partial effects are computed over the estimation sample with standard errors obtained by the delta method. The linear benchmark is the two-way fixed-effects specification of Table 3. The Mundlak test is the joint hypothesis that the four firm means are zero.

Table 4. Fractional response estimates with Mundlak correction.

	Index coefficient	Average partial effect	z	Linear benchmark
TANG	−0.8425*** (0.0332)	−0.2144*** (0.0084)	−25.39	−0.2410*** (0.0102)
SIZE	−0.1683*** (0.0095)	−0.0428*** (0.0024)	−17.71	−0.0437*** (0.0025)
COVER	0.0255*** (0.0015)	0.0065*** (0.0004)	16.69	0.0069*** (0.0004)
GROWTH	0.0406*** (0.0052)	0.0103*** (0.0013)	7.78	0.0103*** (0.0015)
Mundlak test, χ²(4)	609.2***
Observations	73,662
Firms	11,265

Note. Dependent variable: short-term debt over total debt. Fractional probit estimated by quasi-maximum likelihood with the firm mean of each time-varying regressor added as a Mundlak correction, year effects, and standard errors clustered at firm level, reported in parentheses. *** p < 0.01, ** p < 0.05, * p < 0.10. Average partial effects are computed over the estimation sample with standard errors obtained by the delta method. The linear benchmark is the two-way fixed-effects specification of Table 3. The Mundlak test is the joint hypothesis that the four firm means are zero.

The two columns agree. The average partial effect of tangibility is −0.214 against a linear estimate of −0.241: the same sign, the same order of magnitude, and a difference of 0.027 that is about two and a half standard errors of the fractional estimate. The three controls are indistinguishable across the two specifications to the third decimal. The reason the linear model performs this well despite the mass point is visible in the fitted values: only 0.72 per cent of them fall outside the unit interval, because the conditional mean over most of the covariate space is far from either boundary and the pile-up at unity reflects firms that hold no long-term debt rather than a censoring of an underlying latent variable. The regime gradient also survives the change of functional form, with average partial effects of −0.269 for ordinary SMEs, −0.171 for innovative SMEs and −0.110 for innovative start-ups, against −0.312, −0.177 and −0.120 in the linear specifications of Appendix B.

Two implications follow. First, the reported coefficient is not an artefact of imposing linearity on a bounded outcome, which is the concern the boundedness raises. Second, the linear estimate is if anything the more conservative of the two in the direction that matters for the regime comparison, since the fractional model compresses the ordinary-SME slope more than the certified ones and therefore narrows the gap the article emphasises. The linear specification is retained as the baseline because it is directly comparable with the between, dynamic and instrumented estimates that follow, none of which has a standard fractional counterpart.

The controls behave as the same theory requires. Larger firms hold less short-term debt, and the size coefficient is six times larger within firms than across them (−0.0437 against −0.0091), meaning that growth in a firm’s own asset base opens access to long maturities in a way that being structurally large does not capture. Better interest coverage is associated with more short-term debt, not less, which is the sign the refinancing-risk argument predicts: a firm that comfortably services its charges can bear the rollover exposure that a fragile one cannot. Revenue growth pushes weakly in the same direction.

One asymmetry inside the sample deserves recording here rather than only in the appendix, because it is the finding most specific to these populations. Estimating the same within-firm equation separately on the three regulatory groups gives −0.312 for ordinary SMEs, −0.177 for innovative SMEs and −0.120 for innovative start-ups, and a single pooled equation with regime interactions rejects equality of all three slopes at one per cent. The ordering is not a size effect in disguise: the split by size in Appendix B moves the coefficient far less than the split by regime, and the certified firms are on average younger and smaller but also more liquid and less levered. What the gradient says is that maturity matching is a choice, and choosing requires a long-maturity market to be open. A firm whose balance sheet is thin in collateralisable assets, and whose bank credit arrives largely through short-horizon lines carrying a public guarantee, faces a narrower menu, and its maturity structure responds correspondingly less to what it happens to hold in fixed form. Read across the decade the same logic appears in the time dimension, where the cross-sectional slope weakens monotonically from −0.400 in 2016 to −0.348 in 2024.

Two things the static equation cannot do are done in the appendix. It imposes that maturity structure adjusts fully within the year, and it does not. Bounding the coefficient on the lagged dependent variable between the two estimators whose bias is signed places persistence between 0.317 and 0.721; the Anderson–Hsiao estimate of 0.556 lies inside that interval, and the accumulated response to tangibility is −0.437, roughly 1.8 times the static one. And the static equation is associational. Instrumenting the second and third lags of tangibility in first differences returns −0.332 and −0.398 against a first-differenced least-squares benchmark of −0.211, with first-stage F statistics above 979 and a Hansen J of 1.25 at p = 0.263; adding the accumulated depreciation ratio as a third instrument leaves the overidentification test at p = 0.827. Instrumentation therefore moves the estimate away from zero rather than towards it, which is what classical measurement error in a differenced regressor implies, and corroborates the sign without identifying it—the supply-side peer instruments that would have identified it are too weakly correlated with the regressor to be informative, and Appendix C reports them as failures rather than suppressing them.

5. A Taxonomy of Balance-Sheet Configurations

The panel section returned one number for the association between asset composition and debt maturity, and the number is an average. Whether it is the average of one relationship or of several is not something the equation can answer, because the split that would settle it would have to be chosen by the person estimating the equation, and any split chosen that way inherits the hypothesis it is meant to test. This section takes the alternative route. It partitions the same firms on their balance-sheet configuration alone, with the outcome variable of interest treated as one dimension among nine and with the regulatory label withheld entirely, and only afterwards asks whether the groups the data produce differ in the relationship the previous section estimated.

The unit of clustering is the firm rather than the firm-year, because a taxonomy whose members change every year is not a taxonomy; each firm enters as the mean of its own observations over the nine years, and the sample is exactly the 11,265 firms of the panel. The nine dimensions are the nine analysis variables, standardised to zero mean and unit variance so that no dimension dominates by its scale. Six families of algorithms were fitted at five clusters: centroid partitioning, model-based mixture, fuzzy partitioning, agglomerative hierarchy, density-based clustering and an unsupervised random forest. The number five is defended in Appendix D; the short version is that variance explained rises smoothly with no elbow, the information criteria fall monotonically, and the entropy of cluster sizes peaks in the range six to seven, so the choice is a judgement about interpretability rather than a discovery, and it is held fixed across all six algorithms so that the comparison is between algorithms and not between granularities. See Table 5.

Eleven validity indices were computed on every solution, in the same nine-dimensional space and on a common five-thousand-firm subsample wherever a full distance matrix would have been required. They fall into four groups that do not measure the same thing, which is the reason for using all of them: variance criteria (R², Calinski–Harabasz), likelihood criteria (AIC, BIC), geometric criteria (silhouette, maximum diameter, minimum separation, Dunn, Pearson gamma) and balance criteria (the entropy of the size distribution and its Herfindahl–Hirschman concentration). See Table 6.

Reading eleven indices down a column is laborious. The figure recodes each cell by its rank, so the pattern that produces the aggregate ordering becomes visible at a glance. See Figure 3.

The last row of Table 5 is the reason the exercise uses eleven indices rather than one. The density-based solution wins the silhouette outright at 0.250, wins the Dunn index by a factor of four, wins the minimum separation by a factor of nearly three, has the smallest maximum diameter and the lowest information criteria in the table—and it achieves all of this by refusing to classify 35.8 per cent of the firms and by dividing the remainder into two groups that explain 0.4 per cent of the variance. Every geometric index rewards it precisely because discarding the firms that sit between groups is what makes the surviving groups compact and separated. The variance and balance criteria expose it: R² of 0.004, Calinski–Harabasz of 14 against 905 for K-means, a Herfindahl of 0.539. A selection rule built on any single geometric index would have chosen the least informative partition in the set.

Aggregating ranks across all eleven indices puts fuzzy C-means first at a mean rank of 2.62, K-means second at 2.88 and Ward third at 3.17, with the density-based solution fourth precisely because its geometric victories are offset by its balance and variance failures. The gap between the top three is small and none of the substantive results below changes if K-means is substituted; fuzzy C-means is selected because it is first on the aggregate, because it dominates K-means on minimum separation, Dunn, entropy and concentration while conceding only R² and silhouette by two thousandths, and because the membership degrees it produces make the fuzziness of the partition observable rather than hidden. See Figure 4.

The two components account for 47.2 per cent of total variance and identify what the taxonomy is organised around. The first contrasts interest coverage, profitability, capital turnover and short-term debt against tangibility—an operating-intensity axis, running from asset-heavy and slow to asset-light and fast. The second contrasts liquidity against leverage, with size loading negatively on both—a financial-structure axis. Neither is a size axis, which matters: the groups are not a disguised sorting by scale. See Table 7.

Table 7. Cluster profiles.

	C0 Loss-making asset builders	C1 Young and asset-light	C2 Levered traders	C3 Capitalised performers	C4 Capital-intensive
Firms	1,293	2,019	2,942	2,150	2,861
Share of sample	11.5%	17.9%	26.1%	19.1%	25.4%
Short-term share	0.724	0.881	0.890	0.890	0.653
Tangibility	0.461	0.217	0.157	0.231	0.475
ln total assets	6.58	5.29	8.42	8.97	8.91
Interest coverage	−1.89	3.09	3.22	5.38	2.64
Revenue growth	0.612	0.643	0.178	0.103	0.129
Leverage	0.533	0.615	0.818	0.434	0.710
Liquidity	2.33	2.01	1.26	2.81	1.20
Capital turnover	0.45	1.15	1.76	1.03	0.82
Return on assets	−19.03	11.92	5.59	12.37	3.22
Certified share	91.9%	92.6%	14.1%	26.7%	32.5%

Note. Means of firm averages on the raw scale. “Certified share” is the proportion of innovative start-ups and innovative SMEs; the regulatory label took no part in the clustering.

Table 7. Cluster profiles.

	C0 Loss-making asset builders	C1 Young and asset-light	C2 Levered traders	C3 Capitalised performers	C4 Capital-intensive
Firms	1,293	2,019	2,942	2,150	2,861
Share of sample	11.5%	17.9%	26.1%	19.1%	25.4%
Short-term share	0.724	0.881	0.890	0.890	0.653
Tangibility	0.461	0.217	0.157	0.231	0.475
ln total assets	6.58	5.29	8.42	8.97	8.91
Interest coverage	−1.89	3.09	3.22	5.38	2.64
Revenue growth	0.612	0.643	0.178	0.103	0.129
Leverage	0.533	0.615	0.818	0.434	0.710
Liquidity	2.33	2.01	1.26	2.81	1.20
Capital turnover	0.45	1.15	1.76	1.03	0.82
Return on assets	−19.03	11.92	5.59	12.37	3.22
Certified share	91.9%	92.6%	14.1%	26.7%	32.5%

Note. Means of firm averages on the raw scale. “Certified share” is the proportion of innovative start-ups and innovative SMEs; the regulatory label took no part in the clustering.

Table 8. The panel equation estimated inside each cluster.

Cluster	β (TANG)	SE	Obs.	Firms	R² within
C0 Loss-making asset builders	−0.0890***	(0.0308)	5,566	1,293	0.033
C1 Young and asset-light	−0.1728***	(0.0237)	8,602	2,019	0.069
C2 Levered traders	−0.2574***	(0.0189)	21,303	2,942	0.097
C3 Capitalised performers	−0.2373***	(0.0219)	16,746	2,150	0.124
C4 Capital-intensive	−0.2902***	(0.0193)	21,445	2,861	0.130
All firms	−0.2410***	(0.0102)	73,662	11,265	0.092

Note. Dependent variable: short-term debt over total debt. Each row is a separate two-way fixed-effects regression estimated on the firms assigned to that cluster, with the controls of Table 3 (SIZE, COVER, GROWTH) and standard errors clustered at firm level, reported in parentheses. *** p < 0.01, ** p < 0.05, * p < 0.10. Clusters are the fuzzy C-means solution of Table 6, estimated on nine standardised balance-sheet dimensions with the regulatory register withheld. The five cluster slopes are not equal: a pooled equation with cluster interactions rejects equality with a Wald statistic of 56.36 on four degrees of freedom (p < 0.001). Because the clusters were formed on dimensions that include both variables entering the equation, the slope differences are descriptive rather than an out-of-sample test.

Table 8. The panel equation estimated inside each cluster.

Cluster	β (TANG)	SE	Obs.	Firms	R² within
C0 Loss-making asset builders	−0.0890***	(0.0308)	5,566	1,293	0.033
C1 Young and asset-light	−0.1728***	(0.0237)	8,602	2,019	0.069
C2 Levered traders	−0.2574***	(0.0189)	21,303	2,942	0.097
C3 Capitalised performers	−0.2373***	(0.0219)	16,746	2,150	0.124
C4 Capital-intensive	−0.2902***	(0.0193)	21,445	2,861	0.130
All firms	−0.2410***	(0.0102)	73,662	11,265	0.092

Note. Dependent variable: short-term debt over total debt. Each row is a separate two-way fixed-effects regression estimated on the firms assigned to that cluster, with the controls of Table 3 (SIZE, COVER, GROWTH) and standard errors clustered at firm level, reported in parentheses. *** p < 0.01, ** p < 0.05, * p < 0.10. Clusters are the fuzzy C-means solution of Table 6, estimated on nine standardised balance-sheet dimensions with the regulatory register withheld. The five cluster slopes are not equal: a pooled equation with cluster interactions rejects equality with a Wald statistic of 56.36 on four degrees of freedom (p < 0.001). Because the clusters were formed on dimensions that include both variables entering the equation, the slope differences are descriptive rather than an out-of-sample test.

This is the result the section exists to deliver. A taxonomy estimated with no knowledge of the regulatory status of any firm, and with the dependent variable entering as one of nine equally weighted dimensions, reproduces the ordering that the regime split of the panel section produced. The two clusters that are more than nine-tenths certified, C0 and C1, carry the flattest maturity-matching slopes at −0.089 and −0.173; the three clusters dominated by ordinary SMEs carry slopes between −0.237 and −0.290. The steepest is C4, where tangibility averages 0.475 and only 65 per cent of debt is short-term—firms that hold long assets and have arranged long liabilities against them. The flattest is C0, where tangibility is almost as high, at 0.461, but interest coverage is negative and return on assets is −19 per cent: firms that own the collateral and cannot use it, because a lender does not extend a ten-year claim against a borrower who is not covering this year’s charges. Maturity matching, on this evidence, is not a mechanical property of the asset side. It requires both the assets and the standing to borrow against them, and the taxonomy separates the firms that have both from the firms that have only the first.

It is worth being precise about what this does and does not establish. The clusters were built on nine dimensions that include both variables entering the equation, so the slope differences in Table 4 are not an out-of-sample validation and no causal weight attaches to them. What they do rule out is a specific alternative account of the panel result. If the flatter slope among certified firms were produced by the certification process itself—by selection into the register, by the reporting incentives it creates, or by the guarantee schemes attached to it—then a partition built from accounting data alone, blind to the register, would have no reason to reproduce it. It reproduces it exactly: the correlation between a cluster’s certified share and its maturity-matching slope is monotone across all five groups. The more economical explanation is that certification selects firms whose balance sheets already have this shape, and that the shape, not the certificate, is what flattens the slope.

One qualification belongs here rather than in the appendix. The partition is genuinely fuzzy: the mean maximum membership degree is 0.603 and 52.1 per cent of firms have a leading membership below 0.6, so the majority of firms sit somewhere between two configurations rather than inside one. The boundaries are soft, the centres are not, and Appendix G shows that the five centres are stable across bootstrap replication with cluster-wise Jaccard between 0.88 and 0.95.

6. Machine-Learning Regression as a Validation of the Panel Model

The panel estimates rest on an assumption that the estimates themselves cannot test: that every regressor enters linearly and that their effects add. If the true surface curves, or if tangibility matters more when coverage is weak, the fixed-effects coefficient is an average over a structure it does not describe, and nothing in a t statistic would reveal it. This section tests the assumption on the same equation, the same four regressors and the same 73,662 observations, using flexible learners whose accuracy is measured out of sample. The purpose is neither prediction nor identification. It is to establish how much systematic variation the linear form fails to capture, which variables carry it, and whether the omission can be repaired inside a parametric model. Cross-validation is five-fold and grouped by firm, so no firm contributes to both training and testing and the reported accuracy is not inflated by the panel structure.

One comparison made routinely in applied work is invalid, and correcting it changes the size of the result by more than the choice of learner does. The fixed-effects estimator explains variation within firms, after firm and year means have been removed; a learner fitted to raw levels also has the between-firm variation available, which in these data is the larger part. Setting a within R² of 0.075 against a levels R² of 0.290 attributes to functional form what is mostly a different variance decomposition. The two must be placed on the same footing, so every learner is fitted three times: on levels, on levels augmented with firm means in the manner of Mundlak, and on firm- and year-demeaned data, which is exactly what the two-way fixed-effects estimator uses. See Table 9.

Figure 5. Out-of-sample accuracy of six learners under three variance decompositions. Note. Five-fold cross-validation grouped by firm; bars are means across folds and whiskers are one standard deviation. Right: the linear model against the best learner on each footing, with the ratio above each pair.

Figure 5. Out-of-sample accuracy of six learners under three variance decompositions. Note. Five-fold cross-validation grouped by firm; bars are means across folds and whiskers are one standard deviation. Right: the linear model against the best learner on each footing, with the ratio above each pair.

On raw levels the non-linear model is 1.40 times more accurate; on the data the fixed-effects estimator actually uses, the ratio falls to 1.27 and the absolute gap falls from 0.083 to 0.020. The honest statement is that the linear specification recovers 0.075 of within-firm variance against 0.095 attainable, not 0.207 against 0.290. Supplying the linear model with firm means as additional regressors raises it only from 0.207 to 0.218, so the between-firm information the learners exploit is itself non-linear in those means—which is a statement about cross-sectional heterogeneity, not about the within-firm relationship this study estimates. See Table 10.

Two features of this table matter more than the ranking. The first is that two of the four flexible learners are worse than the linear model: a single decision tree recovers 0.066 and nearest neighbours 0.062, against 0.075 for least squares. A learner that can represent any function and still loses to a plane is telling us there is little curvature to find and a great deal of noise to overfit—the nearest-neighbour in-sample R² of 1.000 against 0.062 out of sample is that diagnosis in its purest form. The second is that the linear model and the linear support-vector machine, which differ only in loss function, agree to within 0.002, so nothing in the result depends on squared-error loss or on the influence of outlying observations. Gradient boosting is selected as the reference non-linear model: it is the most accurate, it has the smallest overfitting gap of the four flexible learners, and it is roughly forty times faster to fit than the random forest that comes second. See Figure 6.

The validation proper is in the right panel. If the linear form were hiding a threshold, a saturation or a reversal in the focal relationship, the boosting curve would depart from the dashed line, and it does not: the two are almost indistinguishable over the central four-fifths of the distribution, with mild flattening only in the extreme tails, where the demeaned tangibility of a firm has moved by more than twenty percentage points from its own average. Read as an average marginal effect, the boosting surface returns −0.282 for tangibility against the linear −0.254 on the same fold—the same sign, and a magnitude eleven per cent larger, which is the direction the flattening tails imply. The left panel adds the second thing a validation needs: tangibility is the most important variable under both models, so the flexible learner is not achieving its small advantage by reallocating explanatory weight away from the regressor the study is about.

Interactions are the other way a linear additive form can fail, and they are absent. The Friedman H² statistic between tangibility and each control—the share of their joint partial-dependence variation attributable to interaction rather than to the two separate effects—reaches at most 0.030, against a conventional threshold of 0.10 for a material interaction. The decile calibration in Appendix M shows the linear model compressed rather than misspecified: it under-predicts by 0.015 in the top decile and over-predicts by 0.011 in the bottom, while boosting stays within 0.005 throughout. That is the signature of least squares shrinking a predicted range towards the mean, which is what a linear approximation to a slightly curved surface does.

It is worth stating what a 1.27 ratio means beside the numbers usually reported in this literature. Applications of flexible learners to firm-level accounting data routinely report multiples of three, four or five over a linear benchmark, and those multiples are almost always computed on levels, where the learner has the whole cross-section of firm heterogeneity to exploit and the linear model does not. The companion study on profitability in this project found a ratio of 3.7 on demeaned data, and concluded that the linear form was leaving substantial structure unmodelled. The same procedure applied to the same firms with debt maturity as the outcome returns 1.27. The difference is not methodological, since the design is identical; it is a property of the two dependent variables. Profitability inside a firm responds to its cost structure in ways that curve and interact. Maturity composition responds to asset composition in a way that is close to proportional, which is what the matching principle predicts if firms are actually following it, and which is why the same battery reaches a different verdict here.

Cross-validation grouped by firm answers whether the fitted surface transfers to firms the model has not seen. It does not answer whether it transfers to a period the model has not seen, which is the harder question and the one that matters for a relationship the article claims is structural. Splitting the sample at 2020 and fitting only on the earlier window answers it, and the answer sharpens the conclusion rather than merely confirming it.

The linear model transfers forward and the boosting model does not. Least squares recovers 0.0640 of the demeaned variance inside its training window and 0.0771 in the forward window, so its accuracy does not decay at all. Gradient boosting recovers 0.1220 in training and 0.0734 forward, losing two fifths of its fit, and ends up below the linear model out of period. The forward ratio is 0.95 against the 1.27 obtained under grouped cross-validation: the flexible learner’s advantage, already modest, is entirely an artefact of evaluating it on the same years it was fitted to, and disappears once the test is moved forward in time. Forward RMSE differs between the two models in the fourth decimal.

The coefficient is stable as well. Estimated on 2016–2020 the two-way fixed-effects coefficient on tangibility is −0.2205; estimated on 2021–2024 it is −0.2095. The difference of 0.011 is a fifth of a standard error and equality cannot be rejected at any conventional level, z = −0.48. The boosting model’s average marginal effect moves in the same direction and by a similar amount, from −0.191 to −0.172. A relationship that had drifted, or that the earlier window had captured only through a configuration of the credit cycle specific to those years, would not reproduce itself this closely across a break that includes the pandemic, the inflation shock and the end of the negative-rate period.

The conclusion of the module is therefore stronger than adequacy. The linear additive form is not merely a good approximation to the surface a flexible learner finds in these data; it is the specification that generalises better, both across firms and across time, and the parameter it delivers is stable over a period in which the credit environment changed substantially.

The last question is whether the remaining gap can be repaired without abandoning the parametric model, and half of it can. Adding squares raises the within R² from 0.0746 to 0.0765, squares and cubes to 0.0802, and a full cubic expansion with all interactions to 0.0845—that is 50 per cent of the distance to the boosting benchmark of 0.0945, bought with thirty-four terms in place of four. Cubic splines in tangibility alone add nothing at all, and splines in all four regressors become unstable, with a fold-to-fold standard deviation of 0.100 on a mean of 0.034. The reading is that the residual non-linearity is diffuse rather than concentrated in one variable, that no compact parametric repair captures it, and that the four-term linear specification of the panel module is adequate to these data rather than assumed adequate. That is a claim panel papers ordinarily cannot make, and it is the reason this module exists.

7. Discussion

The three modules answer different questions about the same coefficient, and the value of running all three lies in where they disagree.

The static panel result is the least surprising of the set. A negative association between asset tangibility and the short-term share of debt is what the matching principle predicts and what the cross-sectional literature on listed firms has reported for three decades, from Körner (2007) and Cai, Fairchild and Guney (2008) through Alcock, Finn and Tan (2012) to Byun, Lin and Wei (2021). What the design adds is the decomposition. The between estimate of −0.380 is close to the magnitudes that literature reports; the within estimate of −0.247 is not, because that literature has almost never separated the two. Two-thirds of the cross-sectional gradient survives comparing a firm only with itself, which is a stronger confirmation than the raw correlation ever supplied, and the missing third is composition—firms that are permanently asset-heavy differ from firms that are permanently asset-light in ways the equation does not contain.

The dynamic evidence contradicts a maintained assumption rather than a finding. Every paper cited in the preceding section imposes that maturity structure adjusts fully within the accounting year. It does not: persistence is bounded between 0.317 and 0.721 with an Anderson–Hsiao estimate of 0.556 inside that interval, and the accumulated coefficient of −0.437 is 1.8 times the static one. Papers that read a static coefficient as the eventual response, including those using maturity as a regressor in the manner of Dang (2011) or Wang, Wang and Xu (2022), are understating it by roughly a factor of two.

Instrumentation points the same way. First-differenced least squares returns −0.211 against instrumented estimates of −0.332 to −0.480 with first-stage F above 456 and Hansen J passing at p = 0.827. That is the signature of classical measurement error in a differenced regressor, and it means the fixed-effects estimate is a lower bound rather than an upper one. The supply-side peer instruments fail outright, and are reported as failures.

The taxonomy contributes something neither the panel nor the learners can. Built on nine balance-sheet dimensions with the regulatory register withheld, it reproduces the regime gradient exactly: the two clusters more than nine-tenths certified carry slopes of −0.089 and −0.173, the three dominated by ordinary SMEs between −0.237 and −0.290. This weakens the reading that certification itself flattens maturity matching, and strengthens the reading that certification selects firms whose balance sheets already have that shape. The most informative cluster is C0, where tangibility averages 0.461 but interest coverage is negative: the collateral is present and unusable, which is a qualification the collateral literature of Gopalan, Mukherjee and Singh (2016) and Lim, Macias and Moeller (2020) does not make.

Finally, the machine-learning module returns a verdict against the prevailing expectation. Flexible learners typically beat linear benchmarks by multiples of three to five on firm-level accounting data; here the ratio is 1.27, a single decision tree and nearest neighbours are worse than least squares, and no interaction exceeds H² = 0.030. The linear additive form is adequate to these data rather than assumed adequate. See Table 11.

8. Policy Implications

The evaluation literature on Italian credit policy is unusually rigorous and unusually narrow in one respect. Public guarantee schemes have been assessed with regression-discontinuity, survival and eligibility-threshold designs (Boschi, Girardi & Ventura, 2014; de Blasio, De Mitri, D’Ignazio, Finaldi Russo & Stoppani, 2018; Caselli, Corbetta, Rossolini & Vecchi, 2019; D’Ignazio & Menon, 2020; Caselli, Corbetta, Cucinelli & Rossolini, 2021; Lagazio, Persico & Querci, 2021), and mutual guarantee institutions with comparable care (Bartoli, Ferri, Murro & Rotondi, 2013; Gai, Ielasi & Rossolini, 2016). Every one of these studies measures whether credit is obtained, how much, at what price, and whether the firm survives. None measures the term of the credit obtained. The results here suggest that this is the margin on which the schemes leave their clearest trace: within-firm maturity matching is 0.312 among ordinary SMEs and 0.120 among innovative start-ups, and the cross-sectional slope weakens monotonically from −0.400 in 2016 to −0.348 in 2024. A scheme that relieves the level constraint while leaving the horizon constraint intact does something real for liquidity and nothing for refinancing exposure. Reporting the maturity distribution of guaranteed facilities alongside volumes would cost nothing and would settle the question.

The second implication concerns which firms collateral policy can reach. Cluster C0 holds 46.1 per cent of its assets in fixed form—as much as the most capital-intensive group in the taxonomy—yet its maturity-matching slope is the flattest in the sample at −0.089, and its interest coverage is negative. Collateral is present and unusable, because no lender extends a multi-year secured claim to a borrower not covering this year’s charges. Instruments that operate through pledgeability therefore cannot help the firms in this configuration, and the equity and quasi-equity channels documented by Magri (2014), Haro-de-Rosario, Caba-Pérez and Cazorla-Papis (2016), Lee and Jung (2024) and Pisicoli, Marchionne and Beccari (2025) are the relevant margin for them.

Where pledgeability policy can work is the opposite configuration: firms whose assets are economically valuable and legally unpledgeable. The Chinese patent-pledging reforms studied by Dai, Du, Gao, Gu and Wang (2024), Chen, Pan, Qian, Wu and Xia (2026) and Wang (2026), and the evidence of Lim, Macias and Moeller (2020) that intangibles support more debt than the collateral view predicts, indicate that widening the class of pledgeable assets shifts financing outcomes. The finding here specifies what should be measured if such a reform were attempted in Italy: not only whether certified innovative firms borrow more, but whether their maturity structure lengthens towards the ordinary-SME benchmark.

Finally, a supervisory observation. Almost a third of firm-years in this sample—31.3 per cent—carry no long-term debt at all, so their entire debt stock must be renegotiated within twelve months. The rollover mechanisms formalised by He, Lütkebohmert and Xiao (2017), Della Seta, Morellec and Zucchi (2020), Friewald, Nagler and Wagner (2022) and Chaturvedi and Singh (2024) imply that this concentration is a systemic exposure, not merely a firm-level choice. The short-term share is filed for 99.3 per cent of accounts and requires no reconstruction, which makes it one of the cheapest early-warning indicators available to a supervisor, in the spirit of the default-prediction work of Castaldo, De Luca and Barile (2021).

9. Limitations

The design is associational and should be read as such. Instrumentation with the second and third lags of tangibility produces strong first stages and passes overidentification, and it moves the estimate away from zero rather than towards it, which is informative about measurement error; but internal instruments cannot identify a causal parameter. The designs that could—exogenous shocks to the class of pledgeable assets, of the kind exploited by Dai, Du, Gao, Gu and Wang (2024) and Wang (2026)—have no Italian counterpart in this period, and the supply-side peer instruments constructed here are too weakly correlated with the firm-level regressor to be usable. It bounds what any of the three modules can claim.

Measurement imposes a second bound. AIDA does not disaggregate fixed assets into tangible, intangible and financial components, so the focal regressor is fixed-asset intensity rather than tangibility in the strict sense. The alternative construction, which apportions fixed assets by the observed mix of tangible and intangible amortisation, correlates with the primary measure at only 0.666 and leaves the coefficient essentially unchanged; but the literature on intangible capital (Lim, Macias & Moeller, 2020; McGrattan, 2020; Nakatani, 2023; Deng & Liu, 2024) shows that the distinction matters economically, and a perpetual-inventory reconstruction would be a material improvement. The dependent variable carries its own limitation: the filed index is rounded to two decimals, and 31.3 per cent of firm-years sit at the upper bound, so a linear model is fitted to a censored share. Dropping the boundary observations moves the coefficient away from zero, but a fractional-response estimator would be cleaner.

Three sample limitations follow. The certified populations are self-selected into the Business Register, and nothing is observed about firms that qualified and chose not to register (Castaldo, De Luca & Barile, 2021; Croce, Quas & Tenca, 2025). Firm age is recoverable only for the certified populations, covering 31.1 per cent of observations, so it enters as an appendix control rather than a baseline one—a constraint the private-firm literature has generally avoided by working with smaller, better-documented samples (Heyman, Deloof & Ooghe, 2008). And no bank-relationship data are available: which lender, which guarantee, which contract, which collateral pledge. Since the mechanism proposed for the regime gradient runs through guaranteed short-horizon lending, and since local banking structure is known to shape credit terms in Italy and Spain (Minetti, Murro, Rotondi & Zhu, 2019; Fernández-Méndez & González, 2019; Gama, Sol Murta & Vieira, 2024), the interpretation remains an inference from balance sheets rather than a demonstration.

The taxonomy is soft at its boundaries. The mean maximum membership degree is 0.603 and 52.1 per cent of firms fall below 0.6, so cluster assignment for the typical firm is a close call between two configurations, and the whole-partition adjusted Rand index falls to 0.423 in the weakest bootstrap replication. The multi-index selection procedure follows Mikrou and Sapidis (2025) and Viswanathan, Gopinathan and Rengasamy (2026), but no procedure converts a continuum into islands.

Finally, the evidence is one country over one decade of loosening credit. Whether the regime gradient survives a tightening cycle is the question the crisis-period evidence of D’Amato (2020), Corredera-Catalán, di Pietro and Trujillo-Ponce (2021) and Neves, Serrasqueiro, Dias and Hermano (2020) suggests should be asked next.

10. Conclusions

This paper takes as its object a quantity that is measured in every filed account and almost never used as an outcome: the composition of the debt stock across maturities. It is orthogonal to the level of debt by construction and to its price by observation, and it is the margin on which the collateral mechanism should bite hardest, because a lender extends a multi-year secured claim against a machine and a ninety-day line against a receivable.

Three findings survive the full battery. The first is that maturity matching is real inside firms and not merely across them. The between estimator returns −0.380 and the within estimator −0.247, so two-thirds of the cross-sectional gradient that three decades of listed-firm evidence has reported survives comparing a firm only with itself. The remaining third is composition, and quantifying it rather than assuming it away is the contribution of reporting both numbers side by side.

The second is that adjustment is incomplete. Persistence in maturity composition is bounded between 0.317 and 0.721, with an instrumented estimate of 0.556 inside that interval, and the accumulated response to tangibility is −0.437, about 1.8 times the static coefficient. Every static estimate in this literature, including those that use maturity as a regressor for investment, is therefore reading a partial adjustment as though it were the eventual one.

The third is that the relationship is steeply graded by regulatory regime, and that the gradient is a property of balance sheets rather than of certificates. Ordinary SMEs match at −0.312, innovative SMEs at −0.177, innovative start-ups at −0.120. A taxonomy estimated on nine accounting dimensions, with the register withheld entirely, reproduces the same ordering across its five configurations. Certification selects firms whose balance sheets already have this shape; it does not create the shape. The most instructive configuration is the one in which tangibility is high and interest coverage negative—collateral present and unusable—where the slope is flattest of all. Maturity matching requires both the assets and the standing to borrow against them.

Two methodological conclusions follow from the design rather than from the coefficient. Selecting a clustering algorithm on a single validity index would have chosen, in these data, the partition that explains 0.4 per cent of the variance by discarding 35.8 per cent of the firms; eleven indices and rank aggregation avoid that outcome, and the reason to report the failure is that it is not obvious from any one statistic. And flexible learners, fitted to exactly the variation the fixed-effects estimator uses, improve on the linear specification by a factor of 1.27 rather than the multiples of three to five that the same procedures return on levels, with no interaction exceeding a Friedman H² of 0.030. The linear additive form is adequate to these data rather than assumed adequate, which is a claim panel papers ordinarily cannot make and the reason the third module exists.