# Comparables Pricing

Comparables Pricing Abstract Finance professionals commonly set prices based on the analysis of recently closed, comparable transactions. Using data on syndicated loans, we exploit the lag between loans’ closing dates and their inclusion in a widely used comparables database to identify the effect of past transactions on new transaction pricing. Comparables pricing is an important determinant of individual loan spreads, but a failure to account for overlap in information across loans leads to pricing mistakes. Comparables used repeatedly are overweighted as they develop redundant channels of influence on later transactions. Market conditions prevailing at the time a comparable was priced also unduly influence subsequent loans. Received May 23, 2016; editorial decision January 23, 2018 by Editor Robin Greenwood. Comparables pricing, a valuation method in which agents pricing new transactions explicitly weight the prices of similar, recently closed deals, is arguably the dominant approach to pricing in initial public offerings, mergers and acquisitions, loan and bond markets, real estate, venture capital, and private equity. Given its prominence across a range of markets and the sheer size of those markets, this simple approach to valuation plays a large role in how prices are formed in the economy, yet there is little previous research to help us understand its implications. In this paper, we quantify the effect of comparables analysis on equilibrium prices and show that it can result in prices that are biased in predictable ways. At first glance, it may appear easy to motivate comparables pricing as a form of optimal observational learning—agents pricing new transactions incorporate the private information of others in the economy through the examination of past transactions. Yet, we argue that the correct use of comparables is, in fact, nontrivial and that a basic rule-of-thumb implementation can lead to pricing errors. In particular, suppose that agents aggregate all available information—public and private—when setting prices in any given period. Then all transactions priced during that period would reflect the same shared set of public information, though different pieces of private information. Any attempt to aggregate the private information in recently closed transactions (say, by taking some sort of average of their prices) risks overweighting the public information that is shared across comparables. Properly accounting for this interdependence requires complicated and counterintuitive adjustments to the otherwise-straightforward pricing method.1 At the same time, failing to make these adjustments leads to prices that are wrong conditional on the available information. In this paper, we use the market for corporate loans as a laboratory to explore how agents use comparables to form prices and the implications for equilibrium pricing dynamics. We show that comparables are an important determinant of individual loan spreads in practice, but that a failure to correct for the overlapping information across loans leads to pricing mistakes. The loan market provides an ideal setting in which to study the role of comparables in price formation for a variety of reasons. Unlike the stock market, for example, where prices are set more continually, the rate-setting process for a new loan provides an obvious, salient moment at which the price is set, allowing us to more cleanly identify the effect of comparables on subsequent prices. It is also a market where we observe a large volume of new issuance transactions in any given year. Finally, in this market we can accurately identify when information on pricing terms of past transactions became available to other market participants, which allows us to overcome an immediate identification challenge. Specifically, the interest rate spread of a new loan may be correlated with those of recently closed transactions through two channels: either because the new loan explicitly weighted the past transactions, or because they were jointly influenced by the same economic fundamentals. The first contribution of the paper is to separately identify these two channels using information on when loan terms were made available to nonparticipant banks and were thus eligible to be used broadly for pricing new loans. We use the timing of publication of loan terms to a widely used comparables database as a shock to the information set of lead arranger banks. This allows us to estimate the influence a loan spread has on subsequent transactions as its covariation with spreads on similar loans after being publicly revealed (capturing a causal effect plus the effect of common fundamentals) minus the covariation with similar deals occurring before the comparable was known to the market (the effect of common fundamentals).2 By focusing on within-comparable variation in influence before versus after reporting, we also net out potentially confounding effects of loans that went unreported due to unobservable characteristics that might make them less relevant to subsequent transactions. We find that the interest rate spread on an individual comparable has an average influence of 6–10% on the rate set on subsequent loans. Given these magnitudes, we show that any hypothetical pricing errors would have significant spillovers on related transactions in a world with repeated and recursive use of comparables. Armed with the ability to identify the influence a comparable has on new transactions, we turn our attention to a series of tests that discriminate between optimal use of comparables and a form of naïve inference that treats individual comparables as independent signals. To motivate these tests, consider the following instructive example of a hypothetical series of syndicated loans in a particular industry together with their comparables, consisting of similarly rated borrowers in the same industry. For each of the three loans, we report a truncated list of comparables that a lead arranger might have used when pricing the transaction. Figure 1 reflects the standard practice of using a handful of recent transactions as comparables for each new transaction. Figure 1 View largeDownload slide Recursive use of comparables The figure shows a hypothetical sequence of related transactions and their corresponding comparables. Figure 1 View largeDownload slide Recursive use of comparables The figure shows a hypothetical sequence of related transactions and their corresponding comparables. Note that, upon closing, each transaction joins its own comparables in the set of potential comparables for the next transaction. This highlights an immediate potential source of overlapping information. Specifically, the private information used to price Alpha Inc. influences the price of Bravo Group. Then, when agents price Charlie Corp., the prices of both Bravo Group and Alpha Inc. reflect that same private information. By the time Delta Ltd. is priced, all three comparables shown in the figure share the information originally used to price Alpha Inc. Absent complicated adjustments to account for the redundancy of that information, the Alpha Inc. transaction will effectively be triple counted by the agents pricing Delta Ltd., as a result of its previous influence on both Bravo Group and Charlie Corp. Whereas we have no reason to believe the relevance of Alpha Inc. to each subsequent transaction should be increasing (indeed, it is more likely to be decreasing due to the passage of time), a simple prediction based on naïve inference is that its influence will, in fact, grow with repeated use as a comparable. We test this prediction for our sample of loans and matched comparables and find that the influence of a comparable evolves as it is matched to more and more new transactions, as we would expect if lenders fail to account for information overlap. Whereas a comparable is given a weight of roughly 7% by the first transaction for which it might be informative, its influence grows to 13–15% by the time it has matched to five or more transactions. This pattern is difficult to reconcile with a fully rational model of learning. While the influence of a comparable on a new transaction should be independent of how many intervening transactions there happen to be, the results described earlier suggest that bankers may not be properly accounting for the multiple channels of influence that arise from the recursive use of comparables. To isolate this mechanism directly, we again exploit variation in loan reporting dates. This time, however, rather than simply counting the times a comparable might have been used, we identify actual paths of influence on subsequent loans and then use reporting dates along those paths as a shock to the potential magnitude of information overlap. We begin by searching our data for loan triplets like Alpha, Bravo, and Charlie in the earlier example, where, with prompt reporting, the first transaction would have served as a comparable for the second, and both transactions would have served as comparables for the third. Thus, as in the case of Alpha, Bravo, and Charlie, Alpha stands to influence Charlie both directly and indirectly by way of the intervening loan to Bravo. We then measure the actual number of paths of influence a loan like Alpha could have on Charlie based on (i) whether or not it was reported in time to influence Bravo, and (ii) whether or not Bravo was reported in time to pass that redundant influence on to Charlie. Although it is difficult to conceive of an environment where the appropriate influence of the first loan on the third depends on its use as a comparable for intervening transactions or the reporting of those transactions, we find this is indeed the case. Using the earlier example, Alpha’s influence on Charlie is three to five percentage points higher when Alpha is reported in time to influence Bravo, and Bravo is reported in time to influence Charlie. This constitutes a substantial portion of the baseline level of influence for the average comparable of 6–10% presented earlier. Consequently, equilibrium prices are determined not only by the relevant information available in the market, but also, in large part, by the history of that information’s use. In addition to using comparables, lenders consider the history of macroeconomic conditions when setting interest rates. Yet, to the extent those conditions are persistent, they may already be accounted for in the prices of their comparables. Thus, macroeconomic conditions constitute a second source of redundant information that bankers might potentially overweight when using comparables. Returning to the example from Figure 1, prevailing macroeconomic conditions at the end of 2010 will influence all three comparables for Delta. If that information is subsumed by contemporaneous conditions accounted for directly by Delta’s banker, then through naïve use of comparables, the banker may inadvertently (over)weight stale macroeconomic news. Our final tables show that, in addition to being influenced by contemporaneous macroeconomic conditions, spreads on new loans are influenced by the macroeconomic environment that prevailed at the time their comparables were priced. That is, spreads are lower when comparables were priced in good economic times, holding fixed current conditions. These effects are economically significant. A doubling of the average spread on comparables due to aggregate variation in Baa–Aaa spreads, stock market dividend/price ratios, or aggregate volatility at the time comparables closed translates into a 57% increase in a new loan’s spread relative to loans priced at the same point in time but based on different comparables. As before, this suggests that prices depend not only on the set of information available to agents, but also on how prior agents used that information. Finally, using dealer quotes on a subset of the affected loans that trade in an increasingly liquid secondary market, we find that loans priced at high (low) interest rates based on the influence of stale macroeconomic information via their comparables tend to appreciate (depreciate) in value in the six to twelve months post-issuance, affirming our interpretation of the observed dependence on lagged macroeconomic conditions as an error in at-issue pricing. Our paper builds on a number of important papers across a broad range of research areas. Use of comparables as a pricing methodology has received some attention, notably within the literature on initial public offerings (IPOs). Kim and Ritter (1999) and Purnanandam and Swaminathan (2004) both examine IPO pricing and performance through the lens of comparables analysis. Our paper is also related to the literature on information aggregation in settings characterized by social learning, beginning with the theoretical work on rational herding by Bikhchandani, Hirshleifer, and Welch (1992) and Banerjee (1992), with complementary empirical work on herding among investment newsletters and security analysts (Graham 1999; Welch 2000). More recently, Da and Huang (2016) show that herding results in inferior earnings forecasts. Our focus on the consequences of agents incorrectly treating past transactions as independent signals is most closely related to what DeMarzo, Vayanos, and Zwiebel (2003) and Eyster and Rabin (2010, 2014) term “persuasion bias” or “naïve herding,” respectively. Glaeser and Nathanson (2017) develop and test a model of house prices in which agents make similar inferential mistakes. Finally, the paper relates to the literature on credit cycles and rate setting behavior of banks (Rajan 1994; Ruckes 2004; Dell’Ariccia and Marquez 2006; Gorton and He 2008). Even done properly, comparables pricing has interesting implications for credit dynamics—backwards-looking pricing implies slow credit recoveries after recessions and aggressive lending into deteriorating fundamentals. We also contribute to a growing body of theory and evidence that variation in credit pricing may result from biases in the formation of expectations by lenders (Greenwood and Hanson 2013; Bordalo, Gennaioli, and Shleifer 2018; Dougal et al. 2015). 1. Hypothesis Development In this section, we describe a stylized economic environment to motivate and analyze the use of comparables pricing. The purpose is to develop intuition about the proper use of comparables and to motivate testable predictions that will help us distinguish between optimal and naïve use of comparables in the data. To fix ideas, define comparables pricing as a method of valuing an asset by weighting recent transactions on similar assets (the comparables) and private information about the asset value. We begin by describing the conditions under which comparables pricing is optimal. We then show that in a more realistic information environment, comparables pricing results in suboptimal prices. In particular, agents overweight any information that is redundant across comparables at the expense of nonredundant information. Consider a setting in which prices of assets ($$p$$) are driven by a latent economic factor $$F$$ that we will refer to as “fundamentals.” Fundamentals are persistent and have dynamics given by $$F_t = \rho F_{t-1} + v_t, \label{fundamentals}$$ (1) where $$v$$ is Gaussian white noise with variance $${\sigma}^2_v.$$ In each period an agent needs to estimate fundamentals in order to value an asset. The agent’s objective is to get the value of the asset right, and he is penalized for pricing errors in either direction. For convenience, assume that the penalty for getting prices wrong is symmetric and quadratic so that the agent sets prices based on an unbiased, minimum mean-squared-error estimate of $$F$$; that is, $$p_t=\hat{F_t}$$. In setting prices, agents have access to the full history of prices set by others. Each agent collects information about the asset and about the state of the economy, resulting in a signal of fundamentals given by $$s_t = F_t + u_t, \label{signal}$$ (2) where $$u$$ is Gaussian white noise with variance $${\sigma}^2_u$$ and is independent of $$v$$. Given the signal, the full history of prices, and the understanding that yesterday’s prices were set rationally, the best estimate of fundamentals is given by a simple application of the Kalman filter. Prices are formed recursively by updating the last period’s price to account for new information: $$p_t = w_t \times \rho p_{t-1} + (1-w_t) \times s_t, \label{recprices}$$ (3) where $$w_t$$ is a precision weight and converges to a constant in the steady state.3 Two points are worth emphasizing. First, since optimal prices are a precision-weighted average of past prices and current information, comparables pricing (done correctly) is optimal. Of course, the agent needs to assign the correct weights to past transactions and to his own signal, but in this simple setting these weights are readily accessible. Second, as (3) makes clear, only the most recent transaction should receive any explicit weight. This is because $$p_{t-1}$$ fully reflects all of the information available through time $$t-1$$. Instead of using a single comparable as prescribed by Equation (3), in practice, agents typically use several past transactions, perhaps motivated by the notion that separate transactions contain independent information. While this notion is incorrect in the simple environment with one transaction each period, in more general settings it is not difficult to justify.4 In general, the information embedded in the price of any potential comparable can be partitioned into a component that is unique to that comparable and a component that overlaps with the information available in other comparables. Using multiple comparables may serve to aggregate the independent pieces of information but also introduces the risk of double-counting information that is redundant across those transactions. If agents fail to account for the complex aggregation of information represented by their comparables, in what (testable) ways do we expect their mistakes to manifest? To answer this question, consider a special case of Equation (1) with $$\rho=1$$ and $${\sigma}^2_v=0$$, so that each agent simply estimates an unobservable constant F using a private signal and past transactions. There are three periods and four transactions, with two transactions occurring at time 2. Our interest is in the pricing of the final transaction, D. Panel A of Figure 2 shows the signal received by each agent. At time 1 the only available information in the economy is the first signal, so the agent uses that to price transaction A. The agent pricing transaction B equally weights his own signal of 1.4 and transaction A’s price of 0.6 to arrive at a price of 1.0. The agent pricing transaction C follows the same process to arrive at a price of 0.9. Figure 2 View largeDownload slide Comparables pricing example Each panel in the figure shows a sequence of transactions with their corresponding signals and prices. Signals are noisy estimates of the latent fundamentals that agents are trying to match with their prices. Time starts at $$t=1$$, so transaction A’s price equals its signal. Later transactions are able to observe prior transactions (except where noted in panel C). Our interest is the pricing of transaction D, for which the pricing equation is written out on the bottom of each panel. Signals are the same across all panels, but prices depend on whether agents use comparables optimally and whether each past transaction is observable. Figure 2 View largeDownload slide Comparables pricing example Each panel in the figure shows a sequence of transactions with their corresponding signals and prices. Signals are noisy estimates of the latent fundamentals that agents are trying to match with their prices. Time starts at $$t=1$$, so transaction A’s price equals its signal. Later transactions are able to observe prior transactions (except where noted in panel C). Our interest is the pricing of transaction D, for which the pricing equation is written out on the bottom of each panel. Signals are the same across all panels, but prices depend on whether agents use comparables optimally and whether each past transaction is observable. At the time transaction D is priced, there are four total signals available in the economy, each of which should receive an optimal weight of 0.25 (since each is equally informative to D, given our assumption that $$\rho=1$$ and $${\sigma}^2_v=0$$). Of course, since each comparable presents independently useful information, the observability of any one comparable will also hold sway over the final transaction pricing. For example, because A has the lowest price of the three comparables, removing it from the available information set will raise prices in subsequent transactions. Our first and most basic tests in the paper confirm this prediction, with a focus on specific magnitudes of influence. Prediction 1: Prices vary based on which past transactions were reported and when they were reported. But now note that, assuming all transactions were reported, to correctly price D using comparables, a sophisticated agent would need to negatively weight transaction A (as shown in the pricing equation for transaction D), since prices of B and C already account for signal A. The need to negatively weight transactions when using multiple comparables is quite general; this is a central point in Eyster and Rabin (2014). Any time that multiple comparables were influenced by a common piece of information, the source of that common information must be anti-imitated. This can be very complicated when the common source of information was a shared comparable, since the shared comparable will generally comprise a complex aggregation of information, only some of which needs to be anti-imitated. Anti-imitating shared comparables, then, can lead to over-anti-imitating some information, necessitating still further corrections. In short, getting pricing right with multiple comparables is both difficult and counterintuitive. In contrast to the optimal use of comparables, panel B illustrates naïve pricing of transaction D by an agent who views past transactions as if they were simply signals. In this case, the agent weights each past transaction and his own signal equally.5 Obviously, the price of D is wrong, given the incorrect weighting of information. Naïve use of comparables leads to the information in A being overweighted at the expense of information in B and C. Moreover, this naïve use of comparables results in prices that are not uniquely determined by the set of information in the economy. Instead, prices depend on who used which transactions as comparables in the past. To see this, consider panel C, where we examine the pricing that obtains from naïve inference in a modified case where the relevant signals are unchanged, but we assume that it is common knowledge that B did not use transaction A in its pricing. Comparing panels B and C, the final influence of signal A on D (and the resulting price for D) depends on how many intervening agents chose A as a comparable. This gives us our first two related predictions regarding naïve inference, which we test in Tables 3 and 4: Prediction 2a: Comparables will become more influential with each repeated use. Prediction 2b: Comparables that were used to price more intervening co-comparables will be more influential. Table 3 Repeated comparable use Combined Unreported comps Reported comps Loan spread (1) (2) (3) (4) (5) Comp Spread 0.632*** 0.579*** 0.675*** (0.033) (0.055) (0.024) Comp Spread $$\times$$ 2nd Match (Unreported) –0.023 –0.024 (0.029) (0.023) Comp Spread $$\times$$$$\geq$$ 3rd Match (Unreported) –0.037 –0.008 (0.045) (0.028) Comp Spread $$\times$$ 1st Match (Reported)a 0.066** 0.068*** (0.030) (0.026) Comp Spread $$\times$$ 2nd Match (Reported) 0.075** 0.071** (0.035) (0.031) Comp Spread $$\times$$ 3rd Match (Reported) 0.130*** 0.104*** (0.037) (0.035) Comp Spread $$\times$$ 4th Match (Reported) 0.133*** 0.117*** (0.042) (0.040) Comp Spread $$\times$$$$\geq$$ 5th Match (Reported)b 0.149*** 0.128*** (0.047) (0.043) (b)–(a) 0.083*** 0.060** Comp Spread $$\times$$ Number Prior Matches –0.020 0.022*** 0.020** (0.027) (0.008) (0.009) Number Prior Matches 0.079 –0.103** –0.106** (0.139) (0.041) (0.047) Other Controls YES YES YES YES YES Comp Fixed Effects NO YES NO NO YES Number of Comparables 2,990 2,990 2,990 2,990 2,990 Number of Observations 17,319 17,319 5,433 11,886 11,886 $$R^2$$ 0.502 0.770 0.472 0.515 0.805 Combined Unreported comps Reported comps Loan spread (1) (2) (3) (4) (5) Comp Spread 0.632*** 0.579*** 0.675*** (0.033) (0.055) (0.024) Comp Spread $$\times$$ 2nd Match (Unreported) –0.023 –0.024 (0.029) (0.023) Comp Spread $$\times$$$$\geq$$ 3rd Match (Unreported) –0.037 –0.008 (0.045) (0.028) Comp Spread $$\times$$ 1st Match (Reported)a 0.066** 0.068*** (0.030) (0.026) Comp Spread $$\times$$ 2nd Match (Reported) 0.075** 0.071** (0.035) (0.031) Comp Spread $$\times$$ 3rd Match (Reported) 0.130*** 0.104*** (0.037) (0.035) Comp Spread $$\times$$ 4th Match (Reported) 0.133*** 0.117*** (0.042) (0.040) Comp Spread $$\times$$$$\geq$$ 5th Match (Reported)b 0.149*** 0.128*** (0.047) (0.043) (b)–(a) 0.083*** 0.060** Comp Spread $$\times$$ Number Prior Matches –0.020 0.022*** 0.020** (0.027) (0.008) (0.009) Number Prior Matches 0.079 –0.103** –0.106** (0.139) (0.041) (0.047) Other Controls YES YES YES YES YES Comp Fixed Effects NO YES NO NO YES Number of Comparables 2,990 2,990 2,990 2,990 2,990 Number of Observations 17,319 17,319 5,433 11,886 11,886 $$R^2$$ 0.502 0.770 0.472 0.515 0.805 The table measures the growth in influence of a comparable as it is matched to an increasing number of new transactions. Columns 1 and 2 interact $$CompSpread$$ with dummies for the number of loans a comparable has matched to before and after being reported. The excluded category is the first pre-reported match. Column 2 adds comparable fixed effects. Columns 3 through 5 estimate the growth in influence parametrically by interacting the comparable’s number of prior matches with $$CompSpread$$. Column 3 does this only for comparables before they are reported, while Columns 4 and 5 focus on the same comparables after they are reported, with and without comparable fixed effects. All regressions include controls for comparable age and precision as well as their interactions with $$CompSpread$$, as described in Table 2. Standard errors are reported in parentheses and are clustered at the level of comparable firm and borrowing firm. ***, **, and * indicate significance at the 1%, 5%, and 10% levels, respectively. Table 3 Repeated comparable use Combined Unreported comps Reported comps Loan spread (1) (2) (3) (4) (5) Comp Spread 0.632*** 0.579*** 0.675*** (0.033) (0.055) (0.024) Comp Spread $$\times$$ 2nd Match (Unreported) –0.023 –0.024 (0.029) (0.023) Comp Spread $$\times$$$$\geq$$ 3rd Match (Unreported) –0.037 –0.008 (0.045) (0.028) Comp Spread $$\times$$ 1st Match (Reported)a 0.066** 0.068*** (0.030) (0.026) Comp Spread $$\times$$ 2nd Match (Reported) 0.075** 0.071** (0.035) (0.031) Comp Spread $$\times$$ 3rd Match (Reported) 0.130*** 0.104*** (0.037) (0.035) Comp Spread $$\times$$ 4th Match (Reported) 0.133*** 0.117*** (0.042) (0.040) Comp Spread $$\times$$$$\geq$$ 5th Match (Reported)b 0.149*** 0.128*** (0.047) (0.043) (b)–(a) 0.083*** 0.060** Comp Spread $$\times$$ Number Prior Matches –0.020 0.022*** 0.020** (0.027) (0.008) (0.009) Number Prior Matches 0.079 –0.103** –0.106** (0.139) (0.041) (0.047) Other Controls YES YES YES YES YES Comp Fixed Effects NO YES NO NO YES Number of Comparables 2,990 2,990 2,990 2,990 2,990 Number of Observations 17,319 17,319 5,433 11,886 11,886 $$R^2$$ 0.502 0.770 0.472 0.515 0.805 Combined Unreported comps Reported comps Loan spread (1) (2) (3) (4) (5) Comp Spread 0.632*** 0.579*** 0.675*** (0.033) (0.055) (0.024) Comp Spread $$\times$$ 2nd Match (Unreported) –0.023 –0.024 (0.029) (0.023) Comp Spread $$\times$$$$\geq$$ 3rd Match (Unreported) –0.037 –0.008 (0.045) (0.028) Comp Spread $$\times$$ 1st Match (Reported)a 0.066** 0.068*** (0.030) (0.026) Comp Spread $$\times$$ 2nd Match (Reported) 0.075** 0.071** (0.035) (0.031) Comp Spread $$\times$$ 3rd Match (Reported) 0.130*** 0.104*** (0.037) (0.035) Comp Spread $$\times$$ 4th Match (Reported) 0.133*** 0.117*** (0.042) (0.040) Comp Spread $$\times$$$$\geq$$ 5th Match (Reported)b 0.149*** 0.128*** (0.047) (0.043) (b)–(a) 0.083*** 0.060** Comp Spread $$\times$$ Number Prior Matches –0.020 0.022*** 0.020** (0.027) (0.008) (0.009) Number Prior Matches 0.079 –0.103** –0.106** (0.139) (0.041) (0.047) Other Controls YES YES YES YES YES Comp Fixed Effects NO YES NO NO YES Number of Comparables 2,990 2,990 2,990 2,990 2,990 Number of Observations 17,319 17,319 5,433 11,886 11,886 $$R^2$$ 0.502 0.770 0.472 0.515 0.805 The table measures the growth in influence of a comparable as it is matched to an increasing number of new transactions. Columns 1 and 2 interact $$CompSpread$$ with dummies for the number of loans a comparable has matched to before and after being reported. The excluded category is the first pre-reported match. Column 2 adds comparable fixed effects. Columns 3 through 5 estimate the growth in influence parametrically by interacting the comparable’s number of prior matches with $$CompSpread$$. Column 3 does this only for comparables before they are reported, while Columns 4 and 5 focus on the same comparables after they are reported, with and without comparable fixed effects. All regressions include controls for comparable age and precision as well as their interactions with $$CompSpread$$, as described in Table 2. Standard errors are reported in parentheses and are clustered at the level of comparable firm and borrowing firm. ***, **, and * indicate significance at the 1%, 5%, and 10% levels, respectively. Of course, to get pricing right, agents would need to keep track of (or estimate) the reporting dates of past transactions in order to know what was observable and when, which may be a high hurdle. If we think it would be too difficult for market participants to keep track of which information is redundant, then maybe we should not be surprised to find them neglecting redundancy. Our final tests, however, isolate a set of information embedded in comparables that almost certainly is common knowledge and, hence, should not be subject to risk of overweighting by good Bayesian lenders. Specifically, to the extent an agent pricing a new transaction is influenced by the current state of the macroeconomy, he ought to understand that the same was also true for the agents pricing his comparables in prior periods. And since information on relevant macroeconomic conditions contemporaneous with the closing of his comparables is readily available, a sophisticated agent should be able to filter out the now-extraneous influence of older macroeconomic news on his comparables. In contrast, if agents use comparables naïvely, stale macroeconomic information will be transmitted to new transactions through their comparables. In Tables 5 and 6, we test this prediction: Prediction 3: New transactions are influenced by the macroeconomic conditions that prevailed at the time their comparables were priced, leading to under- or overpricing at issuance. Table 5 Aggregate dynamics under comparables pricing Panel A—First Stage Average Comp Spread (1) (2) (3) (4) $$\overline{\text{Baa-Aaa Spread}}$$ (at comp closing) 0.248*** 0.113** (0.042) (0.047) $$\overline{\text{Market D/P}}$$ (at comp closing) 36.174*** 13.170* (5.468) (6.878) $$\overline{\text{VIX}}$$ (at comp closing) 1.167*** 0.734*** (0.146) (0.181) $$R^2$$ 0.862 0.862 0.868 0.868 F-statistic (excluded instruments) 35.01 43.47 63.23 21.96 p-value of F-statistic 0.00 0.00 0.00 0.00 Panel B—Second Stage Loan spread (1) (2) (3) (4) Average Comp Spread 0.337* 0.623*** 0.645*** 0.567*** (0.173) (0.167) (0.137) (0.138) Year $$\times$$ Month Fixed Effects YES YES YES YES Rating and Industry Fixed Effects YES YES YES YES Loan Controls YES YES YES YES Number of Months 324 324 300 300 Number of Observations 25,820 25,820 25,374 25,374 Panel A—First Stage Average Comp Spread (1) (2) (3) (4) $$\overline{\text{Baa-Aaa Spread}}$$ (at comp closing) 0.248*** 0.113** (0.042) (0.047) $$\overline{\text{Market D/P}}$$ (at comp closing) 36.174*** 13.170* (5.468) (6.878) $$\overline{\text{VIX}}$$ (at comp closing) 1.167*** 0.734*** (0.146) (0.181) $$R^2$$ 0.862 0.862 0.868 0.868 F-statistic (excluded instruments) 35.01 43.47 63.23 21.96 p-value of F-statistic 0.00 0.00 0.00 0.00 Panel B—Second Stage Loan spread (1) (2) (3) (4) Average Comp Spread 0.337* 0.623*** 0.645*** 0.567*** (0.173) (0.167) (0.137) (0.138) Year $$\times$$ Month Fixed Effects YES YES YES YES Rating and Industry Fixed Effects YES YES YES YES Loan Controls YES YES YES YES Number of Months 324 324 300 300 Number of Observations 25,820 25,820 25,374 25,374 The table reports the first and second stages of a 2SLS model of logged loan spreads on the average of logged comparable spreads using variation from prevailing market conditions at the time of the comparables as an instrument. The unit of observation is the loan being priced. Comparables are matched as described in Section 2.2. Both stages include controls for borrower rating and industry (Fama French 30 industries), the logged loan size, and logged maturity in months. Additionally, the first stage presented in panel A includes the Baa–Aaa spread, the aggregate dividend/price level of the S&P 500, and/or the level of the VIX that prevailed at the time the comparables were priced, averaged over a loan’s comparables, as excluded instruments. Panel A reports the impact of these aggregate pricing signals on the average comparable. Panel B then reports the second stage of the 2SLS model to show how that effect is passed on to the loan being priced. All regressions include monthly time fixed effects as of the loan closing date. Standard errors are reported in parentheses and are clustered at the level of the borrowing firm and month. ***, **, and * indicate significance at the 1%, 5%, and 10% levels, respectively. Table 5 Aggregate dynamics under comparables pricing Panel A—First Stage Average Comp Spread (1) (2) (3) (4) $$\overline{\text{Baa-Aaa Spread}}$$ (at comp closing) 0.248*** 0.113** (0.042) (0.047) $$\overline{\text{Market D/P}}$$ (at comp closing) 36.174*** 13.170* (5.468) (6.878) $$\overline{\text{VIX}}$$ (at comp closing) 1.167*** 0.734*** (0.146) (0.181) $$R^2$$ 0.862 0.862 0.868 0.868 F-statistic (excluded instruments) 35.01 43.47 63.23 21.96 p-value of F-statistic 0.00 0.00 0.00 0.00 Panel B—Second Stage Loan spread (1) (2) (3) (4) Average Comp Spread 0.337* 0.623*** 0.645*** 0.567*** (0.173) (0.167) (0.137) (0.138) Year $$\times$$ Month Fixed Effects YES YES YES YES Rating and Industry Fixed Effects YES YES YES YES Loan Controls YES YES YES YES Number of Months 324 324 300 300 Number of Observations 25,820 25,820 25,374 25,374 Panel A—First Stage Average Comp Spread (1) (2) (3) (4) $$\overline{\text{Baa-Aaa Spread}}$$ (at comp closing) 0.248*** 0.113** (0.042) (0.047) $$\overline{\text{Market D/P}}$$ (at comp closing) 36.174*** 13.170* (5.468) (6.878) $$\overline{\text{VIX}}$$ (at comp closing) 1.167*** 0.734*** (0.146) (0.181) $$R^2$$ 0.862 0.862 0.868 0.868 F-statistic (excluded instruments) 35.01 43.47 63.23 21.96 p-value of F-statistic 0.00 0.00 0.00 0.00 Panel B—Second Stage Loan spread (1) (2) (3) (4) Average Comp Spread 0.337* 0.623*** 0.645*** 0.567*** (0.173) (0.167) (0.137) (0.138) Year $$\times$$ Month Fixed Effects YES YES YES YES Rating and Industry Fixed Effects YES YES YES YES Loan Controls YES YES YES YES Number of Months 324 324 300 300 Number of Observations 25,820 25,820 25,374 25,374 The table reports the first and second stages of a 2SLS model of logged loan spreads on the average of logged comparable spreads using variation from prevailing market conditions at the time of the comparables as an instrument. The unit of observation is the loan being priced. Comparables are matched as described in Section 2.2. Both stages include controls for borrower rating and industry (Fama French 30 industries), the logged loan size, and logged maturity in months. Additionally, the first stage presented in panel A includes the Baa–Aaa spread, the aggregate dividend/price level of the S&P 500, and/or the level of the VIX that prevailed at the time the comparables were priced, averaged over a loan’s comparables, as excluded instruments. Panel A reports the impact of these aggregate pricing signals on the average comparable. Panel B then reports the second stage of the 2SLS model to show how that effect is passed on to the loan being priced. All regressions include monthly time fixed effects as of the loan closing date. Standard errors are reported in parentheses and are clustered at the level of the borrowing firm and month. ***, **, and * indicate significance at the 1%, 5%, and 10% levels, respectively. Table 6 Aggregate dynamics and loan mispricing Panel A: First stage Average Comp Spread (1) $$\overline{\text{Baa-Aaa Spread}}$$ (at comp closing) 0.041 (0.069) $$\overline{\text{Market D/P}}$$ (at comp closing) 29.400*** (10.550) $$\overline{\text{VIX}}$$ (at comp closing) 0.874*** (0.313) Observations 3,330 $$R^2$$ 0.753 F-statistic (excluded instruments) 28.49 p-value of F-statistic 0.00 Panel A: First stage Average Comp Spread (1) $$\overline{\text{Baa-Aaa Spread}}$$ (at comp closing) 0.041 (0.069) $$\overline{\text{Market D/P}}$$ (at comp closing) 29.400*** (10.550) $$\overline{\text{VIX}}$$ (at comp closing) 0.874*** (0.313) Observations 3,330 $$R^2$$ 0.753 F-statistic (excluded instruments) 28.49 p-value of F-statistic 0.00 Panel B: Second stage 3-month 6-month 9-month 12-month Loan Post-Issuance Price Change (1) (2) (3) (4) Average Comp Spread 0.012 0.044** 0.057** 0.062* (0.014) (0.021) (0.025) (0.037) Year $$\times$$ Month Fixed Effects YES YES YES YES Rating and Industry Fixed Effects YES YES YES YES Loan Controls YES YES YES YES Number of Observations 2,909 2,978 2,932 2,824 Panel B: Second stage 3-month 6-month 9-month 12-month Loan Post-Issuance Price Change (1) (2) (3) (4) Average Comp Spread 0.012 0.044** 0.057** 0.062* (0.014) (0.021) (0.025) (0.037) Year $$\times$$ Month Fixed Effects YES YES YES YES Rating and Industry Fixed Effects YES YES YES YES Loan Controls YES YES YES YES Number of Observations 2,909 2,978 2,932 2,824 The table reports the first and second stage of a 2SLS model of loan post-issuance price changes on the average of logged comparable spreads using variation from prevailing market conditions at the time of the comparables as an instrument. Price changes are calculated from the month after loan closing to 3, 6, 9, or 12 months thereafter. Data on loan values come from mark-to-market quotes aggregated across dealers by the Loan Syndications and Trading Association. Observations are at the loan level, and comparables are matched as described in Section 2.2. Both stages include controls for borrower rating and industry (Fama French 30 industries), the logged loan size, and logged maturity in months. Additionally, the first stage presented in panel A includes the Baa–Aaa spread, the aggregate dividend/price level of the S&P 500, and/or the level of the VIX that prevailed at the time the comparables were priced, averaged over a loan’s comparables, as excluded instruments. Panel A reports the impact of these aggregate pricing signals on the average comparable. Panel B then reports how that effect is passed on to the subsequent price changes of the affected loans. All regressions include monthly time fixed effects as of the loan closing date. Standard errors are reported in parentheses and are clustered at the level of the borrowing firm and month. ***, **, and * indicate significance at the 1%, 5%, and 10% levels. Table 6 Aggregate dynamics and loan mispricing Panel A: First stage Average Comp Spread (1) $$\overline{\text{Baa-Aaa Spread}}$$ (at comp closing) 0.041 (0.069) $$\overline{\text{Market D/P}}$$ (at comp closing) 29.400*** (10.550) $$\overline{\text{VIX}}$$ (at comp closing) 0.874*** (0.313) Observations 3,330 $$R^2$$ 0.753 F-statistic (excluded instruments) 28.49 p-value of F-statistic 0.00 Panel A: First stage Average Comp Spread (1) $$\overline{\text{Baa-Aaa Spread}}$$ (at comp closing) 0.041 (0.069) $$\overline{\text{Market D/P}}$$ (at comp closing) 29.400*** (10.550) $$\overline{\text{VIX}}$$ (at comp closing) 0.874*** (0.313) Observations 3,330 $$R^2$$ 0.753 F-statistic (excluded instruments) 28.49 p-value of F-statistic 0.00 Panel B: Second stage 3-month 6-month 9-month 12-month Loan Post-Issuance Price Change (1) (2) (3) (4) Average Comp Spread 0.012 0.044** 0.057** 0.062* (0.014) (0.021) (0.025) (0.037) Year $$\times$$ Month Fixed Effects YES YES YES YES Rating and Industry Fixed Effects YES YES YES YES Loan Controls YES YES YES YES Number of Observations 2,909 2,978 2,932 2,824 Panel B: Second stage 3-month 6-month 9-month 12-month Loan Post-Issuance Price Change (1) (2) (3) (4) Average Comp Spread 0.012 0.044** 0.057** 0.062* (0.014) (0.021) (0.025) (0.037) Year $$\times$$ Month Fixed Effects YES YES YES YES Rating and Industry Fixed Effects YES YES YES YES Loan Controls YES YES YES YES Number of Observations 2,909 2,978 2,932 2,824 The table reports the first and second stage of a 2SLS model of loan post-issuance price changes on the average of logged comparable spreads using variation from prevailing market conditions at the time of the comparables as an instrument. Price changes are calculated from the month after loan closing to 3, 6, 9, or 12 months thereafter. Data on loan values come from mark-to-market quotes aggregated across dealers by the Loan Syndications and Trading Association. Observations are at the loan level, and comparables are matched as described in Section 2.2. Both stages include controls for borrower rating and industry (Fama French 30 industries), the logged loan size, and logged maturity in months. Additionally, the first stage presented in panel A includes the Baa–Aaa spread, the aggregate dividend/price level of the S&P 500, and/or the level of the VIX that prevailed at the time the comparables were priced, averaged over a loan’s comparables, as excluded instruments. Panel A reports the impact of these aggregate pricing signals on the average comparable. Panel B then reports how that effect is passed on to the subsequent price changes of the affected loans. All regressions include monthly time fixed effects as of the loan closing date. Standard errors are reported in parentheses and are clustered at the level of the borrowing firm and month. ***, **, and * indicate significance at the 1%, 5%, and 10% levels. 2. Data and Sample Construction Our empirical work depends on the ability to estimate the causal impact that a comparable’s price has on a new transaction. Yet the economic environment described above suggests that this causal impact will be difficult to identify because of the comparable’s correlation with the agent’s private signal or other unobservable (to the econometrician) information used to price the new transaction. Put plainly, two similar, successive transactions will tend to have similar prices because they are exposed to the same economic fundamentals, even in the absence of direct influence. If we were, then, to naïvely regress prices of new transactions on prices of publicly known comparable transactions, the estimated coefficient would contain both the causal impact of the comparable’s price on the new transaction and any correlation caused by common exposure to fundamentals.6 To separate the two effects, we might look for random variation in past prices that is uncorrelated with fundamentals, but this seems hard to imagine. Instead, we approach the identification problem by looking for an appropriate control group against which to benchmark the effect of comparables on subsequent prices—a placebo group for which there could have been no causal effect, but which would allow us to net out the bias described above. In theory, we could search for two sets of comparables for each transaction being priced. The first set would consist of publicly known transactions that could have been plausibly used by an agent pricing new transactions. The second set would consist of otherwise similar transactions, but which, for some exogenous reason, could not have been used as comparables because they were not observable to the pricing agent. Even better, we might examine the covariation of a single set of comparables with subsequent transactions both immediately prior to and immediately after they are publicly reported. In this idealized setting, subtracting the covariation of current prices with comparables not yet known to the market (the effect of common fundamentals) from the covariation of current transaction prices with comparables prices after the comparables were publicly revealed (the causal effect plus the effect of common fundamentals) would isolate the causal effect of past prices on the prices of new transactions. We do our best to replicate the setting described in the previous paragraph by turning to the corporate loan market. In addition to being a large and important source of capital for firms as well as a significant source of revenue for banks—in 2014, Thomson Reuters reported that new U.S. loan originations totaled $${\}$$2.3 trillion and generated bank fees in excess of $${\}$$12.1 billion (Thomson Reuters 2014 Global Syndicated Loans Review)—the loan market also serves as a natural laboratory to explore comparables use, given that, anecdotally, lenders often justify loan terms based on the analysis of recently closed transactions.7 Meanwhile, since the lead arranger on a new issue loan sets interest rates as of a fixed date, we can more cleanly identify the influence of comparables than we could in, say, the stock market, where prices are set on a more continual basis.8 Moreover, we will also argue that within this market, we know something about when lenders would have become aware of past transactions, giving us the opportunity to vary the observability of a comparable and thus tease out its causal influence. Specifically, we focus on the reporting practices of a widely used loan database and associated trade publication that has been the prevailing source used by lenders to research comparable transactions since the late 1980s. The database, known to practitioners as Loan Pricing Corporation’s Loan Connector (LPC or LPC’s Loan Connector), is familiar to academics when sold in a raw database format as DealScan. In its web-based format, Loan Connector is used as the dominant tool for researching recent market activity, featuring a searchable database of closed loans and their key terms. The population of the database, although partially based on parsing Securities and Exchange Commission (SEC) disclosures made by public borrowers, is also largely driven by lenders who report loans to LPC in order to receive credit in the company’s sister publication Gold Sheets’ quarterly league tables. League tables rank lead arranger banks based on the number and volume of transactions closed. The incentive to be highly ranked in league tables is strong, given that this is often a central component of a bank’s standard pitch book to borrowers. Thus, lenders report their loans, although perhaps not immediately, to the database in order to maximize their placement in league table rankings. Competing products exist globally (notably, LoanWare, linked to Euromoney, is relevant in Europe), but in the United States conversations with active lenders suggest that Loan Connector is by far the dominant source of information for reviewing recent market activity. If LPC is a sufficiently important source of information to lead arrangers pricing new loans, then we can exploit inference about when transactions are included in the database as a source of variation in the set of comparables available to a lender.9 In the extreme, if the banker’s information set were completely determined by LPC’s reporting (and we could observe the timing of LPC’s reporting with 100% accuracy), we would converge on the idealized experiment described, whereby unreported comparables serve as a perfect control group. Of course, in practice, we recognize that LPC reporting dates give us an imperfect control group. Lenders have other information about loan market activity. They will be aware of transactions in which they participated or considered participating. They may have conversations with rival lenders about market activity. Finally, our estimates of LPC reporting dates are themselves noisy. While our identification doesn’t require a one-to-one matching between reporting dates and the information set of a lead arranger, a weak relationship between the two would likely cause us to have low-powered tests and the attendant problems thereof. The idealized experiment described also presumes that delays in LPC’s reporting are as good as random, an assumption that is likely to fail in practice. As we go forward, we will, therefore, wish to be careful to consider the extent to which our proposed methodology is working as we would expect.10 With this in mind, we proceed with a discussion on how we recover the reporting date for loans followed by the details on data construction and regression specifications. 2.1 Recovering reporting dates The key input into our analysis is the date on which loans are reported to the LPC database. To identify this, we lean on the fact that PackageIDs—unique identifiers assigned to each loan package in DealScan—are assigned in the order that loans are recorded in the database. This gives us a perfect rank ordering of when transactions were reported, regardless of when they actually closed. In Figure 3, we show a scatter plot of the PackageIDs and the DealActiveDates (typically the closing date or the effective date of the loan, when legal documents become effective). From this we can see clearly that transactions are not always reported at the time of closing. As an example, note the hanging mass of points with PackageIDs close to 10,000 in the first panel of Figure 3. Given the proximity of their PackageIDs, we know that these deals were reported close to the same time, despite the fact that their actual closing dates range from 1981 to 1992. When were these transactions actually reported? Obviously the answer is not 1981, since there were transactions reported at the same time that did not close until 1992. Instead, if for that group of PackageIDs, at least a few were reported on time, then a sensible estimate of the reporting date would be the latest closing date within the group. In this particular case, that would be January 1992. More generally, this date can be estimated as the upper boundary of the scatter plot. The second panel in Figure 3 illustrates the effect of backfill on this scatter plot by zooming in on the transactions occurring during 2007–08. Each observation is labeled with the date the data were downloaded based on two download vintages (2008 and 2014). Notice clearly that observations on the interior of the scatter plot are reported late and thus only appear in the later vintage of the data, despite the fact that most closed in time for inclusion in the 2008 cut. Figure 3 View largeDownload slide PackageIDs and closing dates The figure shows a scatter plot of PackageIDs and DealActiveDates for the DealScan database. The first panel shows the entire scatter plot with a line estimating the 99th percentile upper boundary. The second panel zooms in on closing dates in 2007–08. In the second panel, dots are labeled with the download vintage (2008 or 2014) of the data. Dots on the interior of the scatter plot were reported late, as none show up in the 2008 vintage of the database. Figure 3 View largeDownload slide PackageIDs and closing dates The figure shows a scatter plot of PackageIDs and DealActiveDates for the DealScan database. The first panel shows the entire scatter plot with a line estimating the 99th percentile upper boundary. The second panel zooms in on closing dates in 2007–08. In the second panel, dots are labeled with the download vintage (2008 or 2014) of the data. Dots on the interior of the scatter plot were reported late, as none show up in the 2008 vintage of the database. Thus, we proceed by estimating the upper boundary of the scatter plot of loan dates and deal identifiers by running a quantile regression of the closing date for the loan on the PackageID and the squared PackageID. The quadratic term allows for the curvature of the boundary. We use a rolling quantile regression estimated at the 99th percentile, where each regression includes 15,000 PackageIDs and the regressions are rolled forward with a step-size of 5,000 observations. Average fitted values from the rolling regressions identify the upper boundary of the plot, shown as the solid blue line in the first panel of Figure 3. Finally, because the 99th percentile is arbitrary, we calibrate the fitted dates such that the median transaction was reported within two weeks of closing in the last full year for which we have data.11 This is based on claims by the data provider that the “majority of transactions” are reported within two weeks. The resulting mapping for each PackageID reflects our estimate of the deal reporting date for every transaction in the data.12 For the full sample, this results in an average reporting delay—the time between closing and the loan being reported—of 66 days, but a standard deviation of just over six months. Over the entire sample period, we estimate that 58% of facilities were reported within one month of their deal closing date, although the timeliness of reporting improves over time. Since 2010, for example, 79% of facilities were reported within of a month of the closing date, whereas in 1990 only 9% of facilities were reported within a month. To confirm the reasonableness of our estimates and to highlight the incentives that drive reporting of loans to a data provider like LPC, Figure 4 shows the mean reporting delay for loans originated in different months of the year. Given that incentives to report loans are determined by the desire to be included in league tables prepared by Thomson Reuters/Gold Sheets using LPC’s database (league tables that are reported widely in the financial press), we expect to see that lenders will report transactions more quickly when prompt reporting is necessary to receive credit for transactions in the year-end and quarter-end league tables. Figure 4 confirms this. Whereas median reporting time is less than three weeks in the final month of each quarter, the median reporting delay extends to 35 days in January, immediately following the year-end league table deadline, as bankers have less incentive to promptly report recently closed transactions. While we do not directly exploit this source of variation in reporting date (Murfin and Petersen (2016) show there exist notable borrower selection effects associated with loan closing dates), it is reassuring that our estimates of reporting dates are consistent with what one would expect given the incentives to report. Figure 4 View largeDownload slide Reporting delay by closing month The figure shows the median delay between the closing date of a loan and our estimated loan reporting date as a function of the month of closing. A quarterly pattern is evident, as loans are reported more quickly the closer they are to quarter end. Figure 4 View largeDownload slide Reporting delay by closing month The figure shows the median delay between the closing date of a loan and our estimated loan reporting date as a function of the month of closing. A quarterly pattern is evident, as loans are reported more quickly the closer they are to quarter end. 2.2 Comparable matching With estimates of the date on which LPC published the terms of various loans to its database, we now can track the influence of these loans on future transactions by other lenders. The next challenge, however, is to identify likely candidate comparables for each new transaction. This is nontrivial. However, in the event that we fail in some or even many cases, this will tend to bias our estimates of a comparable’s influence downwards. To identify sensible comparables, we use a matching algorithm that sorts through transactions closed at least 30 days prior to the closing date of the loan of interest but not more than one year prior to that. The slight lag accommodates the gap between the time a loan is priced and its closing date. Within that subset of loans, we look within industry, using Fama and French’s 30-industry classification (Fama and French 1997), and within loan type, where loan type is a data field that distinguishes term loans from revolvers, commercial paper backup facilities, 364-day facilities, banker’s acceptance lines, and so on. Following the suggestions of practitioners active in the market, we also require that short-term loans match to short-term loans and long-term loans match to long-term loans, where long-term (short-term) is defined as maturities longer than or equal to (shorter than) 60 months. Within these groups, finally, we match based on closeness of Standard and Poor’s long-term debt rating of the issuer, Moody’s corresponding issuer rating, or the average of the two for dual-rated issuers, where averages are constructed based on a numerical rating assignment ranging from 2 (AAA) to 24 (C). Ratings are as of the date of loan closing and are reported by LPC. Of course, this forces us to limit the sample to loans for which the borrower had a long-term issuer rating at the time of closing, but it also gives us freedom to include private firms in the sample for which we do not have accounting information (leverage, for example) on which we might otherwise match firms. By forcing the match to occur along one dimension, we are also able to accommodate fuzzy matches without resorting to weighting matrices to scale distance over multiple dimensions. We ensure that matched transactions are separated by no more than one major ratings category (e.g., a BB+ rated loan can match to loans rated from B+ to BBB+) by requiring that the difference in numerical ratings between matches does not exceed three. We generally think this replicates a natural search procedure an analyst might perform when looking for comparables using LPC’s interface—search by industry and loan characteristics, and then look for similarly rated borrowers within that cohort. Using these criteria, each loan is matched to its nearest acceptable comparables: loans that share an industry, loan type, and maturity class, and have a maximum ratings distance of one major ratings category. Finally, we cap the number of comparables a given loan can have such that the average transaction has five reported matches. In the event of ties, we pick comparables with the closest loan maturity and then closest loan amount. Choosing a specific cap to the number of potential comparables is necessary to avoid transactions with an implausibly large number of matches dominating the sample. Moreover, it is important for our empirical tests that we avoid false positives in our matching algorithm to the extent possible. While the failure to identify actual matches limits our test power by restricting sample size, the erroneous identification of irrelevant matches both reduces power and induces a downward bias in many of our basic tests. Conversations with bankers suggest that a typical transaction would likely consider three to seven comparables. Our baseline results use a cap of seven matches per transaction to deliver an average of five. However, in the Appendix we show that we can cap the number of matches at five or ten (for average match numbers of 3.8 and 6.9, respectively) with limited effect on the paper’s core results. After completing the initial matching exercise, we are left with 26,325 transactions being priced by 25,656 distinct comparables. Each facility has an average of 5.4 comparables (5.0 of which are reported, by design), with a maximum of seven and a minimum of one. The average comparable, meanwhile, is used to price 5.5 loans (5.1 loans after being reported). Finally, to sharpen our categorization of which comparables were visible and which were invisible to a given lead arranger, for our initial tests we also drop any observations where the lead arranger of the new transaction was in the syndicate for its comparable. The loan characteristics of the transactions being priced and their matched comparables are presented in panel A of Table 1. We see that, with the exception of loan size, the two groups are on average very similar, at least in terms of maturity, ratings, and spreads. This is not surprising; after all, today’s new transaction will serve as tomorrow’s comparable. The only material difference—loan size—can be explained by the combination of growth in nominal issuance sizes over time and the fact that comparables must occur before matched transactions. Table 1 Summary statistics Panel A Facilities priced Comparables N Mean Median S.D. N Mean Median S.D. $$\Delta$$ Means Facility Amount ($${\}$$M) 23,934 491.8 250.0 870.9 23,108 462.3 235.0 802.1 –29.5*** Maturity (months) 23,934 50.17 60 24.13 23,108 50.11 60 23.97 –0.06 Numerical Avg LT Debt Rating (2-24) 23,934 13.40 14 3.53 23,108 13.41 14 3.47 0.01 Loan Spread 23,934 204.9 175.0 153.3 23,108 206.0 175.0 152.9 1.11 Panel B Unreported comparables Reported comparables N Mean Median S.D. N Mean Median S.D. $$\Delta$$ Means Facility Amount ($${\}$$M) 3,966 318.3 150.0 588.7 22,132 468.1 250.0 807.5 149.8*** Maturity (months) 3,966 44.74 48 24.02 22,132 50.29 60 23.87 5.55*** Numerical Avg LT Debt Rating (2-24) 3,966 13.37 14 3.39 22,132 13.41 14 3.47 0.04 Loan Spread 3,966 183.6 150.3 136.6 22,132 206.4 175.0 152.9 22.8*** Panel A Facilities priced Comparables N Mean Median S.D. N Mean Median S.D. $$\Delta$$ Means Facility Amount ($${\}$$M) 23,934 491.8 250.0 870.9 23,108 462.3 235.0 802.1 –29.5*** Maturity (months) 23,934 50.17 60 24.13 23,108 50.11 60 23.97 –0.06 Numerical Avg LT Debt Rating (2-24) 23,934 13.40 14 3.53 23,108 13.41 14 3.47 0.01 Loan Spread 23,934 204.9 175.0 153.3 23,108 206.0 175.0 152.9 1.11 Panel B Unreported comparables Reported comparables N Mean Median S.D. N Mean Median S.D. $$\Delta$$ Means Facility Amount ($${\}$$M) 3,966 318.3 150.0 588.7 22,132 468.1 250.0 807.5 149.8*** Maturity (months) 3,966 44.74 48 24.02 22,132 50.29 60 23.87 5.55*** Numerical Avg LT Debt Rating (2-24) 3,966 13.37 14 3.39 22,132 13.41 14 3.47 0.04 Loan Spread 3,966 183.6 150.3 136.6 22,132 206.4 175.0 152.9 22.8*** Panel C Switching comparables N Mean Median S.D. Facility Amount ($${\}$$M) 2,990 313.6 150.0 565.2 Maturity (months) 2,990 44.27 47 23.36 Numerical Avg LT Debt Rating (2-24) 2,990 13.30 14 3.29 Loan Spread 2,990 179.1 150.0 131.1 Panel C Switching comparables N Mean Median S.D. Facility Amount ($${\}$$M) 2,990 313.6 150.0 565.2 Maturity (months) 2,990 44.27 47 23.36 Numerical Avg LT Debt Rating (2-24) 2,990 13.30 14 3.29 Loan Spread 2,990 179.1 150.0 131.1 Panel D Facilities priced by unreported comparables Facilities priced by reported comparables N Mean Median S.D. N Mean Median S.D. $$\Delta$$ Means Facility Amount ($${\}$$M) 2,216 474.4 202.5 963.6 5,849 477.0 225.0 878.6 2.60 Maturity (months) 2,216 46.10 53.5 24.22 5,849 47.22 55 22.66 1.12 Numerical Avg LT Debt Rating (2-24) 2,216 13.11 14 3.49 5,849 13.25 14 3.44 0.14 Loan Spread 2,216 183.9 150.0 144.7 5,849 189.8 175.0 140.4 5.90 Panel D Facilities priced by unreported comparables Facilities priced by reported comparables N Mean Median S.D. N Mean Median S.D. $$\Delta$$ Means Facility Amount ($${\}$$M) 2,216 474.4 202.5 963.6 5,849 477.0 225.0 878.6 2.60 Maturity (months) 2,216 46.10 53.5 24.22 5,849 47.22 55 22.66 1.12 Numerical Avg LT Debt Rating (2-24) 2,216 13.11 14 3.49 5,849 13.25 14 3.44 0.14 Loan Spread 2,216 183.9 150.0 144.7 5,849 189.8 175.0 140.4 5.90 The table reports means, medians, and standard deviations of loan amount, maturity, rating, and interest rate spread in basis points. Panel A shows the statistics for the entire sample of loans and their matched comparables as described in Section 2.2 along with a test for equality of means between the facilities being priced and the comparables. Panel B reports the same for the samples of comparables which were or were not reported in time for use. Panel C reports the statistics for the subset of comparables which match to subsequent transactions at least once before and after being reported. Panel D compares the characteristics of the facilities that match to those comparables from panel C before they were reported versus after they were reported, ignoring any transactions that matched to both. ***, **, and * indicate significance at the 1%, 5%, and 10% levels, respectively. Table 1 Summary statistics Panel A Facilities priced Comparables N Mean Median S.D. N Mean Median S.D. $$\Delta$$ Means Facility Amount ($${\}$$M) 23,934 491.8 250.0 870.9 23,108 462.3 235.0 802.1 –29.5*** Maturity (months) 23,934 50.17 60 24.13 23,108 50.11 60 23.97 –0.06 Numerical Avg LT Debt Rating (2-24) 23,934 13.40 14 3.53 23,108 13.41 14 3.47 0.01 Loan Spread 23,934 204.9 175.0 153.3 23,108 206.0 175.0 152.9 1.11 Panel B Unreported comparables Reported comparables N Mean Median S.D. N Mean Median S.D. $$\Delta$$ Means Facility Amount ($${\}$$M) 3,966 318.3 150.0 588.7 22,132 468.1 250.0 807.5 149.8*** Maturity (months) 3,966 44.74 48 24.02 22,132 50.29 60 23.87 5.55*** Numerical Avg LT Debt Rating (2-24) 3,966 13.37 14 3.39 22,132 13.41 14 3.47 0.04 Loan Spread 3,966 183.6 150.3 136.6 22,132 206.4 175.0 152.9 22.8*** Panel A Facilities priced Comparables N Mean Median S.D. N Mean Median S.D. $$\Delta$$ Means Facility Amount ($${\}$$M) 23,934 491.8 250.0 870.9 23,108 462.3 235.0 802.1 –29.5*** Maturity (months) 23,934 50.17 60 24.13 23,108 50.11 60 23.97 –0.06 Numerical Avg LT Debt Rating (2-24) 23,934 13.40 14 3.53 23,108 13.41 14 3.47 0.01 Loan Spread 23,934 204.9 175.0 153.3 23,108 206.0 175.0 152.9 1.11 Panel B Unreported comparables Reported comparables N Mean Median S.D. N Mean Median S.D. $$\Delta$$ Means Facility Amount ($${\}$$M) 3,966 318.3 150.0 588.7 22,132 468.1 250.0 807.5 149.8*** Maturity (months) 3,966 44.74 48 24.02 22,132 50.29 60 23.87 5.55*** Numerical Avg LT Debt Rating (2-24) 3,966 13.37 14 3.39 22,132 13.41 14 3.47 0.04 Loan Spread 3,966 183.6 150.3 136.6 22,132 206.4 175.0 152.9 22.8*** Panel C Switching comparables N Mean Median S.D. Facility Amount ($${\}$$M) 2,990 313.6 150.0 565.2 Maturity (months) 2,990 44.27 47 23.36 Numerical Avg LT Debt Rating (2-24) 2,990 13.30 14 3.29 Loan Spread 2,990 179.1 150.0 131.1 Panel C Switching comparables N Mean Median S.D. Facility Amount ($${\}$$M) 2,990 313.6 150.0 565.2 Maturity (months) 2,990 44.27 47 23.36 Numerical Avg LT Debt Rating (2-24) 2,990 13.30 14 3.29 Loan Spread 2,990 179.1 150.0 131.1 Panel D Facilities priced by unreported comparables Facilities priced by reported comparables N Mean Median S.D. N Mean Median S.D. $$\Delta$$ Means Facility Amount ($${\}$$M) 2,216 474.4 202.5 963.6 5,849 477.0 225.0 878.6 2.60 Maturity (months) 2,216 46.10 53.5 24.22 5,849 47.22 55 22.66 1.12 Numerical Avg LT Debt Rating (2-24) 2,216 13.11 14 3.49 5,849 13.25 14 3.44 0.14 Loan Spread 2,216 183.9 150.0 144.7 5,849 189.8 175.0 140.4 5.90 Panel D Facilities priced by unreported comparables Facilities priced by reported comparables N Mean Median S.D. N Mean Median S.D. $$\Delta$$ Means Facility Amount ($${\}$$M) 2,216 474.4 202.5 963.6 5,849 477.0 225.0 878.6 2.60 Maturity (months) 2,216 46.10 53.5 24.22 5,849 47.22 55 22.66 1.12 Numerical Avg LT Debt Rating (2-24) 2,216 13.11 14 3.49 5,849 13.25 14 3.44 0.14 Loan Spread 2,216 183.9 150.0 144.7 5,849 189.8 175.0 140.4 5.90 The table reports means, medians, and standard deviations of loan amount, maturity, rating, and interest rate spread in basis points. Panel A shows the statistics for the entire sample of loans and their matched comparables as described in Section 2.2 along with a test for equality of means between the facilities being priced and the comparables. Panel B reports the same for the samples of comparables which were or were not reported in time for use. Panel C reports the statistics for the subset of comparables which match to subsequent transactions at least once before and after being reported. Panel D compares the characteristics of the facilities that match to those comparables from panel C before they were reported versus after they were reported, ignoring any transactions that matched to both. ***, **, and * indicate significance at the 1%, 5%, and 10% levels, respectively. In our tests, we will measure the influence of comparables on subsequent loans based on variation in the ability to observe a comparable. In an ideal experimental setting, whether or not a loan was reported in time for use as a comparable would be random or as good as random. Unfortunately, panel B of Table 1 suggests this is unlikely. Comparing the characteristics of comparables that were reported in time for use to the set for which reporting delays prevented their use confirms significant differences in loan amount, maturity, and spread. Comparables that were yet to be reported at the time of match were on average $${\}$$150 million smaller, 5.6 months shorter, and 23 basis points cheaper than comparables that were reported at the time of match. This lines up with lender incentives to report in a timely fashion to the extent that larger loans have a bigger impact on lender league table positions. However, this would also seem to undermine the otherwise useful assumption that the delay with which loans are reported drives quasi-random variation in observability. To deal with this, our identification of comparable influence will rely on the sample of loans that served as potential comparables both before and after being reported. By comparing the change in influence within a given comparable around its report date, we avoid confusing fixed characteristics of the comparables that are jointly related to their relevance and their reporting delay with a causal effect of reported status on subsequent influence. Panel C of Table 1 reports the summary statistics for the “switching” sample of 2,990 loans that matched as potential comparables both before and after being reported. By using each comparable as its own control, we mechanically ensure that fixed characteristics across reported and unreported comparables are identical. Finally, panel D reports the characteristics of the facilities matched to either unreported or reported comparables to look for systematic differences (we have excluded any transactions that matched to both unreported and reported comparables, as these overlapping transactions mechanically shrink differences between the two groups). We find the differences in characteristics across the two groups are economically small. Again, this shouldn’t be surprising, given that both sets of loans are being matched to the same set of comparables, just before and after their report dates. 3. Results 3.1 Estimates of comparables influence With comparables in hand, we would like to compare the influence of a given comparable on its matched loan(s) before and after it becomes publicly visible. This gives us the two regressions of loan terms on the terms of comparables needed to identify the causal effect of a comparable—one in which the comparables are hidden and one in which they are visible. Because we are using data in the syndicated loan market, we focus on the all-in-drawn spread over LIBOR (or a similar risk-free rate) as the pricing variable in question. We take logs of loan spreads (and the spreads of candidate comparable loans) so that the variation in comparable spreads is allowed to have a proportionate influence on matched loans. We also attempt to control for the quality of the match between the loan and its comparable. In our basic specifications, we include a control for the log number of days between the loan closing date and the closing date of the matched comparable, which we refer to as $$CompAge$$. We also control for the precision of the comparables, defined as the negative of the natural log of 1+ the number of ratings categories between the comparable and the loan it is being used to price.13 We refer to this measure as $$CompPrecision$$. Each of these measures is interacted with the log of comparable spreads, such that the influence of comparables is allowed to wane over time and as comparables become less precise. Because the comparables of interest in our sample are each matched to at least two subsequent transactions (one before and one after being reported), and because transactions being priced are assigned multiple comparables, the sample of loan $$\times$$ comparable pairs includes a multiplicity of observations associated with both transactions. Meanwhile, borrowers may have several loans being priced in the data and be associated with numerous comparables. We account for this in our inference with double-clustered standard errors based on the identity of the borrowing firm and the comparable firm. In the Appendix, we also replicate our core results using sampling weights designed to give each comparable equal weight in the regressions to ensure our findings are not being disproportionately driven by a few heavily used comparables. Following the methodological choices laid out above, we are finally prepared to identify the effect of observability on comparable influence. Columns 1 and 2 of Table 2 estimate the following specification: \begin{aligned} LoanSpread_i&=\alpha_{pre}+\beta_{pre}CompSpread_j+\gamma _{1,pre}CompSpread_j\\ &\quad\times Precision_{i,j} +\gamma _{2,pre}CompSpread_j\times CompAge_{i,j}\\ &\quad+\gamma _{3,pre}Precision_{i,j} +\gamma _{4,pre}CompAge_{i,j}+\epsilon_{i,j}\\ LoanSpread_i&=\alpha_{post}+\beta_{post}CompSpread_j+\gamma _{1,post}CompSpread_j\\ &\quad \times Precision_{i,j}+\gamma _{2,post}CompSpread_j\times CompAge_{i,j}\\ &\quad +\gamma _{3,post}Precision_{i,j} +\gamma _{4,post}CompAge_{i,j}+\epsilon_{i,j} \label{regspec} \end{aligned} (4) where $$pre$$ and $$post$$ subscripts reference whether or not comparables were reported in time to influence matched transactions. Loan spreads and comparable spreads are both measured in logs and are winsorized at the 1% level. Meanwhile, the measures of $$CompAge$$ and $$Precision$$ are given a mean of zero and standard deviation of one. This allows us to interpret the difference between $$\beta$$ coefficients as the difference in influence for a comparable of average age and precision. Finally, as described in Section 2.2, to ensure differences in coefficients are not driven by differences in comparable characteristics that vary across the samples, $$\beta_{pre}$$ and $$\beta_{post}$$ coefficients are estimated based on the same set of comparables before and after their report dates. Table 2, Columns 1 and 2 report the relevant parameter estimates from the regressions above. Table 2 Comparable influence Unreported comps Reported comps Combined Loan spread (1) (2) (3) (4) (5) Comp Spread 0.610*** 0.737*** 0.638*** 0.635*** (0.034) (0.015) (0.026) (0.041) Comp Spread $$\times$$ Reported Comp 0.103*** 0.104*** 0.058*** (0.026) (0.027) (0.020) Reported Comp –0.447*** –0.444*** –0.309*** (0.134) (0.139) (0.103) Comp Spread $$\times$$ Precision 0.053*** 0.048*** 0.050*** 0.049*** 0.035*** (0.015) (0.011) (0.010) (0.010) (0.009) Comp Precision –0.256*** –0.222*** –0.235*** –0.231*** –0.165*** (0.076) (0.057) (0.052) (0.052) (0.045) Comp Spread $$\times$$ Comp Age –0.068*** –0.037*** –0.049*** –0.036*** (0.017) (0.011) (0.010) (0.008) Comp Age 0.297*** 0.166*** 0.217*** 0.193*** (0.087) (0.058) (0.052) (0.042) Comp Age Dummies (monthly) $$\times$$ Comp Spread NO NO NO YES NO Comp Fixed Effects NO NO NO NO YES Number of Comparables 2,990 2,990 2,990 2,990 2,990 Number of Observations 5,433 11,886 17,319 17,319 17,319 $$R^2$$ 0.471 0.514 0.500 0.501 0.770 Unreported comps Reported comps Combined Loan spread (1) (2) (3) (4) (5) Comp Spread 0.610*** 0.737*** 0.638*** 0.635*** (0.034) (0.015) (0.026) (0.041) Comp Spread $$\times$$ Reported Comp 0.103*** 0.104*** 0.058*** (0.026) (0.027) (0.020) Reported Comp –0.447*** –0.444*** –0.309*** (0.134) (0.139) (0.103) Comp Spread $$\times$$ Precision 0.053*** 0.048*** 0.050*** 0.049*** 0.035*** (0.015) (0.011) (0.010) (0.010) (0.009) Comp Precision –0.256*** –0.222*** –0.235*** –0.231*** –0.165*** (0.076) (0.057) (0.052) (0.052) (0.045) Comp Spread $$\times$$ Comp Age –0.068*** –0.037*** –0.049*** –0.036*** (0.017) (0.011) (0.010) (0.008) Comp Age 0.297*** 0.166*** 0.217*** 0.193*** (0.087) (0.058) (0.052) (0.042) Comp Age Dummies (monthly) $$\times$$ Comp Spread NO NO NO YES NO Comp Fixed Effects NO NO NO NO YES Number of Comparables 2,990 2,990 2,990 2,990 2,990 Number of Observations 5,433 11,886 17,319 17,319 17,319 $$R^2$$ 0.471 0.514 0.500 0.501 0.770 The table estimates the influence of loan interest rate spreads for past closed loans (the “comparables”) on the spreads of subsequent, similar loans before and after the comparables were reported in a widely used transactions database. Observations are at the level of loan $$\times$$ comparable. Spreads of the loans being priced and the comparables are in logs. $$Comp\ Age$$ and $$Comp\ Precision$$ reflect the logged distance in days and –log of 1+ the difference in numerical ratings between the loan and the comparable. Both are standardized to have zero mean and unit standard deviation for ease of interpretation and are interacted with $$CompSpread$$ in all but Column 4. Column 4 controls for comparable age and its interaction with comparable spread via dummies based on age in months. Column 5 includes comparable fixed effects. Standard errors are reported in parentheses and are clustered at the level of comparable firm and borrowing firm. ***, **, and * indicate significance at the 1%, 5%, and 10% levels, respectively. Table 2 Comparable influence Unreported comps Reported comps Combined Loan spread (1) (2) (3) (4) (5) Comp Spread 0.610*** 0.737*** 0.638*** 0.635*** (0.034) (0.015) (0.026) (0.041) Comp Spread $$\times$$ Reported Comp 0.103*** 0.104*** 0.058*** (0.026) (0.027) (0.020) Reported Comp –0.447*** –0.444*** –0.309*** (0.134) (0.139) (0.103) Comp Spread $$\times$$ Precision 0.053*** 0.048*** 0.050*** 0.049*** 0.035*** (0.015) (0.011) (0.010) (0.010) (0.009) Comp Precision –0.256*** –0.222*** –0.235*** –0.231*** –0.165*** (0.076) (0.057) (0.052) (0.052) (0.045) Comp Spread $$\times$$ Comp Age –0.068*** –0.037*** –0.049*** –0.036*** (0.017) (0.011) (0.010) (0.008) Comp Age 0.297*** 0.166*** 0.217*** 0.193*** (0.087) (0.058) (0.052) (0.042) Comp Age Dummies (monthly) $$\times$$ Comp Spread NO NO NO YES NO Comp Fixed Effects NO NO NO NO YES Number of Comparables 2,990 2,990 2,990 2,990 2,990 Number of Observations 5,433 11,886 17,319 17,319 17,319 $$R^2$$ 0.471 0.514 0.500 0.501 0.770 Unreported comps Reported comps Combined Loan spread (1) (2) (3) (4) (5) Comp Spread 0.610*** 0.737*** 0.638*** 0.635*** (0.034) (0.015) (0.026) (0.041) Comp Spread $$\times$$ Reported Comp 0.103*** 0.104*** 0.058*** (0.026) (0.027) (0.020) Reported Comp –0.447*** –0.444*** –0.309*** (0.134) (0.139) (0.103) Comp Spread $$\times$$ Precision 0.053*** 0.048*** 0.050*** 0.049*** 0.035*** (0.015) (0.011) (0.010) (0.010) (0.009) Comp Precision –0.256*** –0.222*** –0.235*** –0.231*** –0.165*** (0.076) (0.057) (0.052) (0.052) (0.045) Comp Spread $$\times$$ Comp Age –0.068*** –0.037*** –0.049*** –0.036*** (0.017) (0.011) (0.010) (0.008) Comp Age 0.297*** 0.166*** 0.217*** 0.193*** (0.087) (0.058) (0.052) (0.042) Comp Age Dummies (monthly) $$\times$$ Comp Spread NO NO NO YES NO Comp Fixed Effects NO NO NO NO YES Number of Comparables 2,990 2,990 2,990 2,990 2,990 Number of Observations 5,433 11,886 17,319 17,319 17,319 $$R^2$$ 0.471 0.514 0.500 0.501 0.770 The table estimates the influence of loan interest rate spreads for past closed loans (the “comparables”) on the spreads of subsequent, similar loans before and after the comparables were reported in a widely used transactions database. Observations are at the level of loan $$\times$$ comparable. Spreads of the loans being priced and the comparables are in logs. $$Comp\ Age$$ and $$Comp\ Precision$$ reflect the logged distance in days and –log of 1+ the difference in numerical ratings between the loan and the comparable. Both are standardized to have zero mean and unit standard deviation for ease of interpretation and are interacted with $$CompSpread$$ in all but Column 4. Column 4 controls for comparable age and its interaction with comparable spread via dummies based on age in months. Column 5 includes comparable fixed effects. Standard errors are reported in parentheses and are clustered at the level of comparable firm and borrowing firm. ***, **, and * indicate significance at the 1%, 5%, and 10% levels, respectively. The takeaway from Columns 1 and 2 of Table 2 is presented visually in Figure 5. We can see that the influence of a comparable, after accounting for its timeliness and ratings differentials, is shifted up by 0.127 after the transaction is publicly reported. If some transactions were well known even before our recovered reporting date (because of noise in our recovery method or through industry channels other than LPC), we can interpret the gap between these two curves as being a lower bound on the average causal influence of a recently closed loan on the price of a new, similar credit. Figure 5 View largeDownload slide Comparable influence by age and reported status The figure plots the predicted marginal effect of $$CompSpread$$ on $$LoanSpread$$ over the range of values for $$CompAge$$, before and after comparables are reported (calculated as the coefficient on $$CompSpread$$ plus $$CompAge$$ times the coefficient on $$CompSpread \times CompAge$$ from Columns 1 and 2 of Table 2). The spread between the two curves captures a lower bound for the average weight attributed to matched transactions, net of the confounding market information which would jointly appear in both $$LoanSpread$$ and $$CompSpread$$. Curves are estimated from the same set of comparables before and after the comparable report date. Dotted lines represent the 95% confidence intervals for the estimated values. Figure 5 View largeDownload slide Comparable influence by age and reported status The figure plots the predicted marginal effect of $$CompSpread$$ on $$LoanSpread$$ over the range of values for $$CompAge$$, before and after comparables are reported (calculated as the coefficient on $$CompSpread$$ plus $$CompAge$$ times the coefficient on $$CompSpread \times CompAge$$ from Columns 1 and 2 of Table 2). The spread between the two curves captures a lower bound for the average weight attributed to matched transactions, net of the confounding market information which would jointly appear in both $$LoanSpread$$ and $$CompSpread$$. Curves are estimated from the same set of comparables before and after the comparable report date. Dotted lines represent the 95% confidence intervals for the estimated values. In the remaining columns of Table 2, we combine the two regressions by allowing the coefficient on $$CompSpread$$ to vary based on whether the comparable has been reported. That is, we estimate: \begin{aligned} LoanSpread_i = &\alpha+\beta_1 CompSpread_j +\beta_2 CompSpread_j\times Reported_{i,j} \\ &+ \beta_3 Reported_{i,j} + \gamma Controls_{i,j} + \epsilon_{i,j} \label{regspec2} \end{aligned} (5) In Column 3, we find the difference, captured in the coefficient on $$CompSpread\times ReportedComp$$, is economically and statistically significant at 0.103. Going from Columns 1–2 to 3, we have also forced the decay rates in comparables over time and across ratings to be the same for reported and unreported transactions. While, as we discuss later, we have reason to think that the reported transactions will have different dynamics, note that allowing the coefficients on $$CompSpread\times CompAge$$ and $$CompSpread\times CompPrecision$$ to differ in Columns 1 and 2 doesn’t materially impact the coefficient of interest. Moreover, we fail to reject a test that the coefficients on $$CompSpread\times CompAge$$ and $$CompAge$$ are jointly equal across Columns 1 and 2 (and similarly for $$CompSpread\times Precision$$ and $$Precision$$). Thus, going forward, we will generally lean on the more parsimonious specification. Column 4 replaces $$CompAge$$ with more flexible dummy variables based on comparable age (in months) with minimal effect on the interaction $$CompSpread\times ReportedComp$$. We emphasize this specification choice in particular because, in theory, this could be an important source of confounding variation. Because, by definition, comparables can never be “unreported” once they are “reported,” $$CompAge$$ naturally covaries with $$ReportedComp$$. Thus, the manner in which we control for comparable age could potentially have a large bearing on the coefficient on $$CompSpread\times ReportedComp$$. However, we find the estimated influence of a comparable to be invariant to allowing for a non-parametric decay function for comparable age. Even though we focus on the same set of comparables before and after they are reported, it is possible that some comparables are more economically relevant and that these transactions are both reported more quickly and merit more influence. Such transactions would be over-represented among the reported comparables, potentially confounding our estimates of the causal influence of a comparable. To address this, Column 5 pushes the within-comp identification strategy to its limit by estimating the specification in Column 3 with the additional inclusion of 2,990 comparable fixed effects. Although the coefficient of interest attenuates substantially in terms of economic significance, dropping from 0.103 to 0.058, the difference is not statistically significant.14 Going forward, we are careful to show results with and without the inclusion of comparable fixed effects where appropriate. One way to interpret the economic magnitude of our estimates is to consider the propagation of any hypothetical pricing errors that might affect a given loan. To do so, consider the following back-of-the-envelope calculation. Since today’s loans become tomorrow’s comparables, if each loan is priced using $$X$$ number of comparables, then the average loan will also influence $$X$$ number of loans subsequently. In our sample, for example, this number is roughly five. As mentioned above, our conversations with bankers suggest that a typical transaction might consider 3–7 similar deals as comparables. Thus, the average loan will also be considered as a comparable for 3–7 transactions. As a result, any pricing error on a given loan will be propagated directly to 3–7 subsequent loans. More importantly, however, the pricing errors induced in those 3–7 loans will spillover to an additional 9–49 loans, and so on. The multiplier effect generated by an individual pricing error under comparables pricing can be approximated by $$\frac{1}{1-Number of Comps\times w_{comp}}$$, where $$w_{comp}$$ is the average causal influence of a comparable.15 Taking $$w_{comp} =0.10$$ as a rough estimate from Table 2 and assuming three comparables are used to price a loan, for example, the multiplier effect is 1.4 times as large as the effect of the initial mispricing. Assuming lenders use 5–7 comps, combined direct and indirect effects are 2.0–3.3 times as large as the direct effects on their own. Recall that, for a variety of reasons, we should interpret the coefficients from Table 2 as lower bounds on the influence of a comparable. As a result, the economic magnitudes discussed here should also be interpreted as lower bounds. It seems reasonable, then, to expect the aggregate effects of a given loan’s mispricing on all borrowers to be around twice as large as the effect on the directly-impacted borrower due to the practice of comparables pricing. To put these multipliers into context, consider recent papers in finance and economics suggesting that interest rates charged by lenders may reflect concerns that go beyond the scope of the current borrower’s creditworthiness. Ivashina (2009), for example, documents that information asymmetry between the lead arranger of a loan and the syndicate explains variation in loan spreads. Her discussion of economic magnitudes suggests typical variation in loan spreads resulting from this channel would amount to 29 basis points (see paper for a deeper discussion). Chodorow-Reich (2014), meanwhile, documents a bank-credit channel in which distressed lenders charge higher rates for relationship borrowers. Representative variation in lender distress, he shows, drives as much as 48 basis points in additional borrowing costs for matched borrowers. The analysis suggests these effects drive hiring decisions at these firms. While these magnitudes are nontrivial on their own, our analysis would suggest the spillover effects of pricing errors on subsequent transactions by other firms may be at least as large, potentially much larger. For example, the substantive 48 basis point increase in borrower spreads documented in Chodorow-Reich (2014) would translate into a cumulative interest rate effect of 68–160 basis points when spread among indirectly affected borrowers. So, although it may be widely accepted that comparables play a role in a variety of markets, Table 2 suggests their direct and indirect spillover effects on equilibrium prices are large in magnitude. Moreover, the results also establish the validity of using loans’ reporting dates as a source of variation for comparable observability. This is a crucial ingredient in our forthcoming tests to determine whether comparables are being used appropriately. 3.2 Tests of naïve use of comparables We now turn our focus to the question of whether the use of comparables in practice looks like optimal information aggregation or naïve herding. None of the results documented to this point imply the mistaken use of comparables. Pricing spillovers are collateral damage from an environment with imperfect information. Yet, as we discussed in Section 1, using comparables appropriately in realistic information environments would be difficult. Lenders would need not only to identify like transactions for use in pricing, but also to recover the basis under which those transactions were priced. In our setting, this requires, at a minimum, that lenders know exactly the path of influence from one loan to another for the entire history of interdependent transactions. Prima facie, this seems unlikely. If, instead, lenders naïvely treat past transactions as if they were independent signals, comparables pricing will result in predictable empirical patterns in which redundant information across comparables is consistently overweighted. The first such empirical pattern that we examine is how the influence of a comparable evolves with repeated use. As a comparable is used repeatedly, the possibility arises that it will have both direct and indirect influence on new transactions. If agents fully take into account the multiple paths of influence, then we would expect the influence of a comparable to be flat as it is used by more and more subsequent transactions, controlling for any decrease in influence due to the passage of calendar time. On the other hand, if agents fail to correct for the possibility that a given loan has directly influenced subsequent loans that are also being used as co-comparables, then we would expect to see the total influence of a loan actually grow in transaction time. That is, as it sequentially influences more and more transactions, naïve lenders will give direct weight to the loan based on its role as a comparable, but also inadvertently allow it additional indirect influence as a progenitor of subsequently closed comparables. Table 3 provides evidence consistent with the latter effect. Returning to the setup and basic controls used in Table 2, we replace the dummy for whether or not a comparable has been reported with a set of dummies that indicate the number of transactions the comparable has been linked to both before and after being reported, allowing us to trace the evolution of influence based on repeated use within a given comparable. In Columns 1 and 2, the specification is: \begin{aligned} LoanSpread_i &= \alpha + \beta CompSpread_j + \sum\limits_{k} \beta_{pre,k} CompSpread_j \\ &\quad \times PreMatchNumberK_{i,j} + \sum\limits_{k} \beta_{post,k} CompSpread_j \\ &\quad \times PostMatchNumberK_{i,j} + \gamma Controls_{i,j} + \epsilon_{i,j}, \label{regspec3} \end{aligned} (6) where the controls, as before, include $$CompAge$$ and $$CompPrecision$$ interacted with $$CompSpread$$ as well as level effects for any interacted variables. The omitted category is the first match pre-reporting, such that in Column 1, for example, the coefficient on $$CompSpread$$ captures the covariation of the average comparable with the first subsequent transaction to which it is matched before it has been reported. The interactions of $$Comp Spread \times 2^{\rm nd} Match (Unreported)$$ and $$Comp Spread \times 3^{\rm rd} Match (Unreported)$$ test whether or not influence is growing before the transaction has been reported. The absence of any trend here is reassuring in that, even under gross misuse of comparables, redundancy should not take effect until after the loan has been reported. In contrast, the coefficients on $$Comp Spread \times 1^{\rm st} Match (Reported)$$ through $$Comp Spread \times \geq 5^{\rm th} Match (Reported)$$ increase monotonically.16 The difference in influence from the first time a comparable is used to the fifth is 0.083, significant at the 1% level and more than double the initial influence. These findings are plotted graphically in Figure 6. The pattern of influence resembles a kinked hockey stick, with a flat region before the comparable is reported, a jump due to the initial influence the first date it is reported, and a trend based on repeated use thereafter. Figure 6 View largeDownload slide Comparable influence with repeated use The figure plots the coefficients for $$CompSpread \times n^{\rm th} Match$$ in Column 1 of Table 3, documenting the evolution of comparable influence with each subsequent match to a newly priced transaction, both before and after the comparable was reported. Figure 6 View largeDownload slide Comparable influence with repeated use The figure plots the coefficients for $$CompSpread \times n^{\rm th} Match$$ in Column 1 of Table 3, documenting the evolution of comparable influence with each subsequent match to a newly priced transaction, both before and after the comparable was reported. Recall that the sample used in Table 3 includes only comparables that match to at least one subsequent transaction both before and after being reported. However, the set of comparables that have a fifth match may differ in important ways from the average comparable. Consider, for example, a comparable that is intrinsically more informative about fundamentals for some unobservable reason. If this comparable is also reported relatively quickly, then it would be more likely to have a fifth match after being reported. Thus, we might worry that more economically relevant comparables are overrepresented among the set with five or more matches, driving the increase in influence that we see with later matches in Column 1. To address this concern, we include comparable fixed effects in Column 2. In doing so, we net out any baseline variation in merited influence associated with a given comparable that could be plausibly correlated with the number of matches assigned to it. That is, the difference in $$Comp Spread \times 1^{\rm st} Match (Reported)$$ and $$Comp Spread \ \times\geq 5^{\rm th} Match (Reported)$$ of 0.060 (significant at the 5% level) captures the change in influence for a given comparable based on potential for repeated use and not the difference in influence across comparables based on the frequency with which our algorithm finds matches. Columns 3–5 estimate linear trends in influence before and after reporting for the same set of comparables. Again, in Column 3, we see no evidence that matching repeatedly to subsequent loans is associated with additional influence. It is not until after the comparable is reported in Columns 4 and 5 (with and without comparable fixed effects) that the trend in influence emerges. The fixed effects results from Columns 2 and 5 significantly restrict the range of possible alternative interpretations. To reconcile these results with a fully rational model of comparables pricing, it would need to be the case that comparables are systematically more relevant for pricing later matches than they are for pricing earlier matches. While it is impossible to rule out that later comparable matches are better along unobservable dimensions, along observable dimensions we find no evidence that match accuracy improves for the later transactions. A test of match distance based on maturity, loan size, and ratings fails to reject the hypothesis of no difference in match quality between a comparable’s first match and its fifth or later matches with a test p-value of 0.66. As a second point of emphasis here, recall that our assigned matches are based on our own algorithm designed to approximate the matches a banker might have chosen for a given deal and not the actual comparables used. Hence, if some transactions are unobservably more relevant and, as a result, are used more frequently in practice by bankers, that variation would not show up in the number of matches captured by our algorithm. Put differently, our inability to observe the actual comparables used by lenders acts as a feature that allows us to rule out the possibility that our results are being driven by lenders who learn about a comparable’s relevance (and thus weight it more heavily) when they see other lenders using it. The growth in comparable influence based on its multiplicity of links to related loans observed in Table 3 would seem consistent with the hypothesis that lenders are bad Bayesians who fail to account for redundant information. At the same time, note that our sharpest prediction regarding the risk of redundancy has to do with the number of potential paths for redundancy, not the simple count of how many times the transaction has been used. These may differ for two reasons. First, consider an A rated transaction which first matches as a comparable for a subsequent A– rated transaction and later matches a second time for an A+ rated transaction. Because the rating of the intervening A– transaction is too distant to match to the later A+ transaction, there is no redundant path of influence from the A rated comparable to the A+ rated transaction. Second, consider a comparable has been used four times before matching to its fifth transaction. It will have five potential paths of influence so long as each of the prior four transactions has been reported by the time the fifth transaction is priced. On the other hand, if none of the intervening transactions have been reported, the comparable can only have a direct path of influence, limiting the possibility of inadvertent overweighting. Following this line of reasoning, we now sharpen our tests of boundedly rational use of comparables by tracking specific paths of influence and exploiting variation in the potential for redundancy based on reporting delays of intervening transactions. For concreteness, consider the picture presented in Figure 7. A, B, and C represent three related transactions, each of which might be identified as an informative comparable for the others. The timing of transactions is such, however, that A precedes B, which precedes C. Finally, assume that A was publicly reported in time to be used by C, but perhaps not in time for B. Moreover, B may or may not have been reported in time to be used in the pricing of C. These variations are captured in the figure with solid lines (implying a given comparable was reported in time for use) and dotted lines (implying it was not). For the triplet (i), note that there is a path for redundancy. Transaction A can be used directly by C, but also may exert indirect influence by way of B. In contrast, for triplets (ii) and (iii), the potential for inadvertently overweighting A is shut down, either because A was not reported in time to influence B$$'$$ (as in (ii)) or because B$$'$$ was not reported in time to influence C$$'$$ (as in (iii)).17 Figure 7 View largeDownload slide Redundant comparables The figure lays the framework for our tests of redundancy bias. A, B, and C represent loan transactions. Solid arrows drawn between loans reflect directional influence, so the line between A and C, for example, suggests that A was a viable (publicly known) comparable for transaction C. In scenario (i), then, A has influence on C both directly and indirectly through B. We refer to A as a redundant comparable for C, and $$\beta_R$$ represents the total influence of A on C. Dotted arrows indicate that our algorithm matched the comparable to the new transaction but that the comparable was not reported in time to actually influence the new transaction. To the right of the vertical line, then, no redundancies occur. In scenario (ii), there is no redundant path of influence from A to C$$'$$ because A was not reported in time to influence B$$'$$. Similarly, A is not redundant for C$$'$$ in scenario (iii) because B$$'$$ was not reported in time to influence C$$'$$. We call A a nonredundant comparable for C$$'$$ and represent its influence with $$\beta_{NR}$$. Figure 7 View largeDownload slide Redundant comparables The figure lays the framework for our tests of redundancy bias. A, B, and C represent loan transactions. Solid arrows drawn between loans reflect directional influence, so the line between A and C, for example, suggests that A was a viable (publicly known) comparable for transaction C. In scenario (i), then, A has influence on C both directly and indirectly through B. We refer to A as a redundant comparable for C, and $$\beta_R$$ represents the total influence of A on C. Dotted arrows indicate that our algorithm matched the comparable to the new transaction but that the comparable was not reported in time to actually influence the new transaction. To the right of the vertical line, then, no redundancies occur. In scenario (ii), there is no redundant path of influence from A to C$$'$$ because A was not reported in time to influence B$$'$$. Similarly, A is not redundant for C$$'$$ in scenario (iii) because B$$'$$ was not reported in time to influence C$$'$$. We call A a nonredundant comparable for C$$'$$ and represent its influence with $$\beta_{NR}$$. To understand the sophistication of the lender, our question revolves around how much total influence transaction A has on C relative to the influence it has on C$$'$$. If lenders incorrectly treat A and B as independent signals, any information contained in the pricing of loan A will be duplicated in B and therefore overweighted by C. Thus, a naïve treatment of comparables will see $$\beta_R>\beta_{NR}$$, as the total influence of A on C aggregates the direct influence and the indirect influence through B. We refer to this as redundancy bias. To implement the tests described above, we begin by searching our matches of loans and their comparables (as described in Section 2.2) for the relationships shown in Figure 7. Specifically, we identify loan triplets $$\{A,B,C\}$$ such that A was used as a comparable for B and C, and B was also used as a comparable for C. We compare these sets of loans to alternative triplets $$\{A,B',C'\}$$ featuring the same comparable of interest (A) and identical linkages, except that at least one of the indirect links (A $$\rightarrow$$ B$$'$$ or B$$'$$$$\rightarrow$$ C$$'$$) is shut down because the comparable was not reported in time to be used by the new transaction. Of course, we also encounter cases in which A has the potential for indirect influence on C through more than one intervening loan (i.e., multiple B transactions that closed between A and C chronologically). A comparable is deemed $$Redundant$$ when it has an indirect effect through at least one such sibling transaction. The spirit of our tests closely matches that of tests in Tables 2 and 3. Specifically, after identifying transactions matching the description above, we regress the spreads of transactions C on the spreads of comparable transactions A interacted with a redundancy dummy: \begin{aligned} LoanSpread_i = &\alpha+\beta_1 CompSpread_j +\beta_2 CompSpread_j\times Redundant_{i,j}\\ &+ \beta_3 Redundant_{i,j} + \gamma Controls_{i,j} + \epsilon_{i,j} \label{regspec4} \end{aligned} (7) We estimate this either in a single model with an interaction term as above, or in separate models with separately estimated coefficients on controls. In either case, as before, we include controls for the age of a comparable interacted with $$CompSpread$$, as well as the precision of the comparable and its interaction. Columns 1 and 2 of Table 4 begin by comparing the influence of the same set of comparables on subsequent transactions with and without a redundant path of influence across two separately estimated regressions. The difference in coefficients on $$CompSpread$$ suggests that the availability of additional paths of influence increases comparable influence by 0.034. Similar magnitudes are seen on the interaction between $$CompSpread$$ and $$Redundant$$ in the combined specifications in Columns 3 and 4, with and without comparable fixed effects. Finally, Columns 5 and 6 take advantage of the variation in the number of paths of influence that a given comparable has over a new transaction by breaking the $$Redundant$$ dummy into a set of dummies based on the number of redundant paths. For example, referring back to Figure 7, A will have two redundancies for C if there are two different B transactions that satisfy the redundant relationship in scenario (i). We see that influence grows with each additional redundancy, growing from 0.015 with the first redundancy to 0.077 by the fourth redundancy in Column 5 and by similar magnitudes in Column 6, where we include comparable fixed effects. One benefit of tracing out the full path of influence of a comparable through potential co-comparables is that it allows us to isolate different sources of variation in the potential for redundancy. In panel A of Table 4, redundancy was driven in part by the reported status of the comparable in question (A), and in part by the reported status of its co-comparables (B) (see Figure 7). In panel B we instrument for $$Redundant$$ using only the reported status of B with respect to C. By eliminating variation in redundancy associated with the visibility of the comparable in question, we rule out a class of explanations that depend on a comparable’s changing relevance being correlated with whether or not it was visible to its co-comparables. Instead, the remaining alternative interpretations—that is, other than redundancy neglect—depend on the seemingly more tenuous assertion that a comparable’s relevance varies with the reported status of peripheral transactions. Columns 1 and 2 of panel B reestimate the regressions from Columns 3 and 4 of panel A. This time, however, we instrument for $$Redundant$$ using an indicator equal to one when redundancy is prevented because no B transactions were reported in time to be used by C (as reflected in scenario (iii) of Figure 7). We call this indicator $$DelayedB$$ for reference. We further use $$CompSpread \times DelayedB$$ as an instrument for $$CompSpread \times Redundant$$ (Wooldridge 2010).18 With the variation in redundancy fully isolated to the reporting status of B transactions, we can control for the reporting delay associated with A (in log days between the transaction and its report date) and its interaction with $$CompSpread$$, which we do in Column 1. Our findings are consistent with the magnitudes presented in panel A, with the instrumented effects of redundancy increasing a comparable’s influence by 0.052. Finally, in our most stringent specification, Column 2 adds back comparable fixed effects. Although the two strategies (using comparable fixed effects and/or instrumenting for cross-comparable variation in redundancy) might be reasonably viewed as substitute identification schemes, even in combination, the effects of redundancy are undisturbed. An alternative approach to these tests, meanwhile, might be to simply limit the sample to scenarios (i) and (iii) in Figure 7, where the A comparable was reported in time for its B co-comparables. Within this restricted sample, the only source of variation in redundancy is the reported status of B transactions (the IV and OLS strategies are equivalent in this subsample since $$DelayedB$$ moves one-for-one with $$Redundant$$). Moving to the restricted subsample drops 12,613 observations for which the comparable under investigation was not reported in time for its potentially intervening B transactions. The interaction $$Redundant \times CompSpread$$ remains positive, significant, and largely unchanged across various specifications. In Column 3, we estimate the regression from Equation 7. In Column 4, we add controls for comparable A’s own reporting delay, interacted with $$CompSpread$$, while in Column 5 we add comparable fixed effects. In each case, redundancy increases a comparable’s influence by between 0.034 and 0.37. Finally, Column 6 reports the growth in influence based on the number of redundancies, again including comparable fixed effects. The growth in influence driven by variation in co-comparables’ report dates is similar to that shown in panel A. In addition to verifying the robustness of findings in panel A by using variation in redundancy that is one transaction removed from the comparable itself, the tests in panel B of Table 4 also help to rule out a subtle reinterpretation of redundancy neglect. Viewed in isolation, panel A cannot rule out the possibility that lenders are aware of the risk of redundancy in their comparables but lack the information on loan observability needed to correct for it. Referring back to Figure 7, it may be that a lender in scenario (i) or (ii) recognizes the potential for redundancy but is unsure whether or not A was reported in time for B. Given this uncertainty, a sophisticated lender could choose weights such that A would receive too much weight in case of an actual redundancy (scenario (i)) and too little weight in the absence thereof (scenario (ii)), but just the right weight on average (scenarios (i) and (ii) together).19 To test whether A receives the right weight on average when the lender perceives a possible redundancy, we might pool the potentially redundant scenarios (i) and (ii) and compare them to scenario (iii), in which there is no apparent risk of redundancy. This is exactly what is done by the instrumental variables specifications in panel B. This is perhaps easiest to see by examining the reduced form regression corresponding to Column 1 of panel B (reported in Column 3 of Table A2 in the Appendix). By isolating the variation in redundancy to that which comes from the reported status of B transactions, we are effectively comparing scenarios (i) and (ii) to scenario (iii). The negative coefficient on $$DelayedB$$ in the reduced form (or the corresponding positive coefficient in the IV regressions) suggests lenders do not just place excess weight on comparables known to the econometrician to be redundant—on average, they overweight the set of comparables that they themselves should recognize to be potentially redundant, even absent information on reporting dates. This, in turn, implies that pricing errors are due to more than just incomplete information on when loans were made available to rival lenders for use as comparables. Lenders are not getting things right on average, but instead make gross errors in information aggregation consistent with redundancy neglect. Table A2 First-stage and reduced-form regressions from instrumental variables specifications in Column 1 of Table 4, panel B Redundant CompSpread $$\times$$ Redundant Loan Spread (1) (2) (3) Comp Spread 0.016*** 0.933*** 0.830*** (0.005) (0.024) (0.015) CompSpread $$\times$$ Delayed B –0.028*** –0.798*** –0.036** (0.008) (0.036) (0.015) Delayed B –0.524*** 0.639*** 0.147** (0.041) (0.170) (0.075) Comp Spread $$\times$$ Precision –0.002 0.001 0.034*** (0.002) (0.011) (0.007) Comp Precision 0.023** 0.048 –0.152*** (0.012) (0.049) (0.038) Comp Spread $$\times$$ Comp Age –0.013** 0.185*** –0.028*** (0.006) (0.029) (0.009) Comp Age 0.317*** 0.319** 0.117*** (0.031) (0.134) (0.045) Comp Spread $$\times$$ Comp Delay –0.001 –0.068*** –0.010** (0.002) (0.007) (0.004) Comp Delay –0.060*** 0.016 0.047** (0.008) (0.033) (0.021) Observations 29,801 29,801 29,801 $$R^2$$ 0.583 0.623 0.625 Redundant CompSpread $$\times$$ Redundant Loan Spread (1) (2) (3) Comp Spread 0.016*** 0.933*** 0.830*** (0.005) (0.024) (0.015) CompSpread $$\times$$ Delayed B –0.028*** –0.798*** –0.036** (0.008) (0.036) (0.015) Delayed B –0.524*** 0.639*** 0.147** (0.041) (0.170) (0.075) Comp Spread $$\times$$ Precision –0.002 0.001 0.034*** (0.002) (0.011) (0.007) Comp Precision 0.023** 0.048 –0.152*** (0.012) (0.049) (0.038) Comp Spread $$\times$$ Comp Age –0.013** 0.185*** –0.028*** (0.006) (0.029) (0.009) Comp Age 0.317*** 0.319** 0.117*** (0.031) (0.134) (0.045) Comp Spread $$\times$$ Comp Delay –0.001 –0.068*** –0.010** (0.002) (0.007) (0.004) Comp Delay –0.060*** 0.016 0.047** (0.008) (0.033) (0.021) Observations 29,801 29,801 29,801 $$R^2$$ 0.583 0.623 0.625 The setup for the redundancy regressions is shown graphically in Figure 7 and discussed in the text. Observations are at the loan $$\times$$ comparable matched pair. Columns 1 and 2 show the first-stage regressions of an indicator for $$Redundant$$ and $$CompSpread \times Redundant$$ on $$DelayedB$$ and $$CompSpread \times DelayedB$$. $$DelayedB$$ is an indicator set to one when none of the co-comparables for a given transaction were reported in time to influence the transaction, thus shutting down the risk of redundancy. Column 3 reports the reduced-form regression suggested by Column 1 of Table 4. Standard errors are reported in parentheses and are clustered at the level of comparable firm and borrowing firm. ***, **, and * indicate significance at the 1%, 5%, and 10% levels, respectively. Table A2 First-stage and reduced-form regressions from instrumental variables specifications in Column 1 of Table 4, panel B Redundant CompSpread $$\times$$ Redundant Loan Spread (1) (2) (3) Comp Spread 0.016*** 0.933*** 0.830*** (0.005) (0.024) (0.015) CompSpread $$\times$$ Delayed B –0.028*** –0.798*** –0.036** (0.008) (0.036) (0.015) Delayed B –0.524*** 0.639*** 0.147** (0.041) (0.170) (0.075) Comp Spread $$\times$$ Precision –0.002 0.001 0.034*** (0.002) (0.011) (0.007) Comp Precision 0.023** 0.048 –0.152*** (0.012) (0.049) (0.038) Comp Spread $$\times$$ Comp Age –0.013** 0.185*** –0.028*** (0.006) (0.029) (0.009) Comp Age 0.317*** 0.319** 0.117*** (0.031) (0.134) (0.045) Comp Spread $$\times$$ Comp Delay –0.001 –0.068*** –0.010** (0.002) (0.007) (0.004) Comp Delay –0.060*** 0.016 0.047** (0.008) (0.033) (0.021) Observations 29,801 29,801 29,801 $$R^2$$ 0.583 0.623 0.625 Redundant CompSpread $$\times$$ Redundant Loan Spread (1) (2) (3) Comp Spread 0.016*** 0.933*** 0.830*** (0.005) (0.024) (0.015) CompSpread $$\times$$ Delayed B –0.028*** –0.798*** –0.036** (0.008) (0.036) (0.015) Delayed B –0.524*** 0.639*** 0.147** (0.041) (0.170) (0.075) Comp Spread $$\times$$ Precision –0.002 0.001 0.034*** (0.002) (0.011) (0.007) Comp Precision 0.023** 0.048 –0.152*** (0.012) (0.049) (0.038) Comp Spread $$\times$$ Comp Age –0.013** 0.185*** –0.028*** (0.006) (0.029) (0.009) Comp Age 0.317*** 0.319** 0.117*** (0.031) (0.134) (0.045) Comp Spread $$\times$$ Comp Delay –0.001 –0.068*** –0.010** (0.002) (0.007) (0.004) Comp Delay –0.060*** 0.016 0.047** (0.008) (0.033) (0.021) Observations 29,801 29,801 29,801 $$R^2$$ 0.583 0.623 0.625 The setup for the redundancy regressions is shown graphically in Figure 7 and discussed in the text. Observations are at the loan $$\times$$ comparable matched pair. Columns 1 and 2 show the first-stage regressions of an indicator for $$Redundant$$ and $$CompSpread \times Redundant$$ on $$DelayedB$$ and $$CompSpread \times DelayedB$$. $$DelayedB$$ is an indicator set to one when none of the co-comparables for a given transaction were reported in time to influence the transaction, thus shutting down the risk of redundancy. Column 3 reports the reduced-form regression suggested by Column 1 of Table 4. Standard errors are reported in parentheses and are clustered at the level of comparable firm and borrowing firm. ***, **, and * indicate significance at the 1%, 5%, and 10% levels, respectively. In summary, across a variety of samples and specifications, we find that allowing the possibility of a redundant path of influence increases the influence of a given comparable by 0.028–0.052. To put these magnitudes in perspective, recall that our earlier tables estimated the average influence attributable to a single comparable to be between 0.058 and 0.104. Hence, when compared with the baseline influence estimated in Table 2, redundancy neglect appears to play a large role in price formation. 3.3 Naïve comparables and aggregate dynamics Our final tests go further in demonstrating the degree to which comparables represent a form of naïve inference and broaden the scope of errors users make. Recall from the examples in Section 1 that common information will tend to be overweighted based on naïve use of comparables. In Tables 3 and 4, common information is shared among comparables based on the recursive use of those comparables. While this is a natural mechanism for generating excess weight on some information at a given point in time, correcting the mistake requires lenders to know exactly what comparables were used, when they were used, and by whom. Now we consider the history of market-wide macroeconomic information from equity and bond markets as a source of common information about fundamentals—in particular, Baa–Aaa bond spreads, the market dividend/price (D/P) ratio, and the VIX index—and test the extent to which naïve inference dictates the dynamic relationship between loan spreads and aggregate conditions. We focus on price signals that are widely available and likely constitute relevant information to the lender pricing a new loan, just as they would have been used by lenders setting terms for comparables. Yet, just as we documented that naïve inference might lead a lender to mis-weight the history of past signals by improperly accounting for their recursive use, the same risk looms large with aggregate signals. Standing at time $$t$$, a lender forms his opinion about fundamentals by examining the entire history of news. This may involve placing positive weight on aggregate levels of Baa–Aaa spreads from the prior month either implicitly (by weighting current Baa–Aaa spreads, which are highly persistent) or explicitly. Yet, if in addition to his best guess of fundamentals based on this history of aggregate news he also weights comparables from the prior month, he may fail to account for the fact that his comparables were also largely influenced by the then-contemporaneous Baa–Aaa spread. Naïve inference generates the prediction that, holding fundamentals constant, loans for which the relevant comparables occurred in good times will benefit from more attractive terms. News about fundamentals will have a persistent effect on prices, where the persistence depends on the frequency with which transactions are completed and used as comparables. Table 5 asks the following: at a given point in time, can cross-sectional variation in loan spreads be explained by variation in the aggregate conditions prevailing at the time relevant comparables were priced? Using the matching methods employed in the previous tables, we generate a sample of matched comparable $$\times$$ loan pairs, this time limiting ourselves to matches that were reported in time to be used as comparables for the current loan. For each loan, we compute the average logged spread of that loan’s comparables, as well as the average of Baa–Aaa spreads, the dividend/price ratio of the S&P 500, and the VIX prevailing at the time each comparable was priced (we again assume loans were priced one month prior to closing).20 For example, assume credit spreads in September, October, and November are 75, 100, and 150, respectively. For a loan being priced in January (Loan 1) using comparables priced in November and October, we would calculate the average spreads prevailing at the time of its comparables as 125. The spirit of our test will be to compare Loan 1 to another simultaneously priced loan (Loan 2) for which we identify comparables that were priced in September. For Loan 2, prevailing credit spreads at the time its comparables were priced were just 75. Based on the differences in aggregate conditions prevailing at the time comparables closed, we would, of course, expect that the comparables for Loan 1 will have higher spreads than those for Loan 2. This is testable, and we report this is the case in panel A of Table 5. And while lenders setting rates for Loans 1 and 2 may optimally wish to use the full history of Baa–Aaa spreads in setting new prices, in doing so, they will need to account for the fact that that October and November’s information was already reflected in the spreads of Loan 1’s comparables, while September’s information was already embedded in the spreads of Loan 2’s comparables. Any evidence of cross-sectional variation in loan spreads based on the prevailing macroeconomic conditions at the time of comparables’ closing would strongly indicate a gross error in the interpretation and use of information embedded in comparables. We report our findings in the form of two-stage least squares (2SLS). As opposed to the traditional motivation for 2SLS as a remedy for endogenous covariates, we use the methodology instead to track and isolate the path of influence of aggregate macroeconomic news. The first stage shows the effect of macroeconomic news on a set of comparables. The second stage shows how that effect, in turn, is transmitted into variation in subsequent loan spreads. The first stage of the 2SLS is presented in panel A of Table 5. The unit of observation is the primary loan being priced, where each loan has been matched to an average of five comparables following the methodology described in Section 2.2. Only comparables that were reported in time to be used are included. The dependent variable in the first stage is the average log spread of comparables we have identified for each loan. The variation of interest is that of prevailing Baa–Aaa spreads, the S&P 500 dividend/price ratio, and the level of the VIX in the month that comparables were priced, averaged over all the comparables for a given loan. In the first stage, we include all controls that we will need in the second stage, including rating and industry fixed effects for the borrower being priced, along with a control for the log of loan size (in dollars) and log of loan maturity (in months). We also include time fixed effects at the monthly frequency, where timing is tied to the closing date of the loan being priced. Many of these controls are motivated by the second stage. We will return to a discussion of them shortly. Columns 1–4 of panel A demonstrate the unsurprising link between the various market indicators and contemporaneous spreads on loans to be used as comparables. In Columns 1–3 we find that Baa–Aaa bond spreads, D/P levels, and the VIX positively covary with the spreads chosen for loan market borrowers. Column 4 includes all indicators jointly. At the bottom of the table, we report the F-statistic testing for significance of the excluded instruments. In each case, they exceed standard rules of thumb (Staiger and Stock 1997) as well as 10% critical values for maximal IV size based on Stock and Yogo (2005). Though the results here are not surprising, they confirm that the macro variables chosen influence contemporaneous loan spreads and with the right signs. High bond spreads generate high loan spreads. Loans priced in periods of low valuation (high D/P) and high volatility also have higher loan spreads. Without sufficient influence of aggregate information on the loan market here, we could not reasonably proceed to test whether or not that information was incorrectly overweighted later by way of comparables. The results from panel B, on the other hand, are more surprising. In the second stage, we now regress the log spread chosen for the new loan on the average log spread, where averages are taken over multiple comparables. But, by construction and the mechanics of 2SLS, the variation in the average spread of the comparables is limited to that which comes from our first stage instruments used in panel A (any other source of variation in the fitted values from the first stage is absorbed by the inclusion of the full set of controls). In other words, Column 1 tells us how new loan pricing is affected by variation in the pricing of comparables that comes from the Baa–Aaa spread at the time of each comparable.21 Before discussing the results, an important aspect of the test we wish to highlight is the presence of monthly fixed effects as of the date of the loan being priced. By including time fixed effects, we can be agnostic about the appropriate use of lagged macroeconomic news. Because the history of lagged macroeconomic news will be the same for all loans priced in a given month, the fixed effects absorb that information completely without needing to specify a particular lag structure. The only variation remaining comes from the timing of when comparables for a given loan occurred. The coefficients in panel B tell us the extent to which a loan puts excess weight on stale information based on the timing of its comparables. Looking across Columns 1–4 of panel B, we see the different effects based on different instrument choices (each column corresponds to the first-stage regression reported in the same column from panel A). Column 1, for example, uses Baa–Aaa spreads occurring in the month of comparables as the sole instrument. We find that a doubling of the average spread on comparables due to aggregate variation in Baa–Aaa spreads at the time of the comparables (holding fixed contemporaneous bond spreads) translates into a 33.7% increase in the affected loan’s spread relative to loans priced at the same point in time but based on different comparables. Columns 2 and 3 repeat the exercise using the dividend/price ratio and the VIX and find larger and more significant effect sizes. Finally, Column 4 uses all three instruments jointly. A doubling of comparable spreads based on common macro signals coming from bond and equity markets increases spreads for loans priced based on those comparables by 56.7%.22 As in Tables 3 and 4, the evidence suggests excess weight is placed on the correlated information contained in comparables, this time due to presumably stale macroeconomic information. But what if loan prices should contain the stale information documented above, or the “stale” information from the time of transaction comparables is more relevant than we think? For example, sleepier segments of the market will have comparables arrive with a longer lag. If the same segments also respond to macroeconomic conditions with a similar lag structure, the patterns in Table 5 may not reflect pricing errors at all. In other words, without random arrival rates of comparables, it is difficult to rule out endogenous matching between the timing of comparables and sensitivity to macro fundamentals. To help sort this out, our last results track the ex post performance of the loans being priced based on the lag structure motivated above. Using a subsample of loans that trade in the secondary market after being priced in the primary market, we calculate the percentage capital appreciation on the loan between the month after the loan closed and 3, 6, 9, or 12 months thereafter. To be conservative, we ignore the component of loan returns attributed to the affected interest rates and focus only on price changes, although results are consistent when loan coupon payments are added to the return. In the event the loan is not traded in the secondary market in the month following the closing date, we instead calculate capital appreciation as the percentage change in price relative to par or, if the loan was issued at a discount, the percentage change in price relative to its discounted issue price over the corresponding time horizon. Data on loan values come from mark-to-market quotes aggregated across dealers by the Loan Syndications and Trading Association. We match these to DealScan using a matching file of deal identifiers provided by Thompson Reuters and some data cleaning. For example, we drop facilities for which the issuance dates across the two data sources differ by more than 60 days. We also drop loans that appear to trade in advance of their DealScan closing date. We should be wary that any test that relies on an active response to mispricing in the secondary loan market may be hampered by stale loan quotes provided by dealers. At the same time, other work suggests a surprising amount of efficiency in the secondary loan market. Addoum and Murfin (2017) show that dealer quotes on secondary loans may even lead the corresponding equities of the same firm. We emphasize that any evidence of predictability by no means suggests a profitable trading strategy. Dealer quotes are not firm and transaction costs may be large. Instead, our tests might be conservatively interpreted as capturing changing dealer opinions about the value of loans after the time of purchase. In panel A, we repeat the first-stage regression from Column 4 of Table 5 to confirm that, even in the limited sample of traded loans, the spreads of the loans’ comparables are predicted by prevailing macroeconomic conditions at the time they closed. Unlike the prior results, the effect of credit spreads is crowded out in the first stage, but otherwise, dividend to price and volatility provide a strong first stage to generate variation in issuance spreads based on comparable conditions. In panel B, we present the second-stage results, which suggest that in the 6, 9, and 12 months after the loan closes, dealer quotes adjust based on the variation in spreads. A doubling of comparable spreads due to prevailing macro conditions predicts 4–6% appreciation in the loan’s value in the 6, 9, and 12 months post issuance. These are nontrivial effect sizes. Twelve-month returns on the loans have a standard deviation of just 8%. Taken together, Tables 5 and 6 document the patterns we might expect from a boundedly rational use of comparables that fails to take into account overlapping information. Over time, loans that were overpriced at the time of issuance tend to fall in value, and vice versa, confirming that the patterns of comparable use present direct evidence of mispricing. These results complement the findings from earlier tables in several ways. First, they again distinguish between an imperfect but still sophisticated use of comparables in which lenders weight comparables such that spreads are right on average, but sometimes overweight and sometimes underweight past information based on the history of comparable use. In such a world, we might think that the cost of tracking who used which comparable to make corrections for signal redundancy is simply too large. Yet whereas the presumption of common knowledge about the history of comparables use may be too large an information burden for even sophisticated users of comparables, common knowledge regarding use of market-wide information should not be. Even boundedly rational lenders should assume that lenders setting terms at $$t-1$$ would have used this information. Thus, the evidence that aggregate movements in bond or equity markets occurring at the time of a comparable’s closing have undue influence over the subsequent loans priced using that comparable suggests a gross pricing error. Table 5 also contributes to our understanding of the complicated dynamics in asset prices that are induced by the use of comparables. Even the correct use of comparables would suggest prices will reflect a moving average of lagged fundamentals. This is consistent with the tendency for average loan spreads to be smoother than bond market yields. That phenomenon, however, might also reflect the smoothing benefits of relationship banking, where lenders overcharge in good times in order to hedge borrowers against bad times. Yet the more complicated dynamics implied by Table 5 suggest that, because lenders incorporate stale macroeconomic news through naïve use of comparables, current prices will tend to overweight lagged fundamentals at the expense of other information. Prices are set based on a distributed lag of aggregate news, where the lag length depends on when transactions relevant to the current batch of new loans last closed. 4. Discussion We have documented the practice and practical importance of comparables pricing in credit origination markets. We show that comparables play a quantitatively important role in the way that credit is priced. Moreover, we find strong evidence that the use of comparables is a manifestation of naïve inference, leading to predictable pricing mistakes and dynamics of credit spreads that depend on the timing of comparables. Given the interest in how credit is allocated, priced, and perhaps mispriced, this is an important avenue for examination. However, the applications of comparables pricing are much broader. IPO markets, real estate, mergers and acquisitions, private equity, and a host of secondary markets all rely heavily on this pricing methodology. The primary lessons from our analysis may extend more broadly to these markets. As the dominant pricing methodology in these markets, how significant is comparables pricing as a driver of pricing dynamics? The evidence of naïveté in the use of comparables suggests interesting policy questions going forward. If agents were using comparables efficiently, then everyone would be made better off by the availability of market information, since prices would be as accurate as possible given available information. However, this is not necessarily true when agents use comparables naïvely. Are there situations in specific markets in which opacity may actually improve pricing accuracy? We leave this and other questions for future research. We thank Nick Barberis, Sudheer Chava, David Hirshleifer, Rodney Ramcharan, Geoffrey Tate, Heather Tookes, participants at the Miami Behavioral Finance Conference, Olin Corporate Finance Conference, Red Rock Finance Conference, and Colorado Finance Summit and seminar participants at Boston College, Brigham Young University, Columbia University, Cornell University, Ohio State University, University of Alberta, University of California San Diego, University of Utah, Yale University, and the Philadelphia Fed for helpful comments. Appendix A. Supporting Tables Table A1 Industry distribution of unreported/reported comparables Major industry group of comparables Unreported Reported Total Food Products 1.79% 2.85% 2.69% Beer and Liquor 0.00% 0.05% 0.05% Tobacco Products 0.00% 0.05% 0.04% Recreation 2.09% 2.39% 2.35% Printing and Publishing 1.11% 1.69% 1.60% Consumer Goods 1.19% 1.70% 1.62% Apparel 0.38% 0.68% 0.63% Healthcare, Medical Equipment, Pharmaceutical Products 5.07% 6.35% 6.15% Chemicals 2.37% 2.80% 2.73% Textiles 1.01% 0.61% 0.67% Construction and Construction Materials 5.90% 3.79% 4.11% Steel Works Etc. 1.39% 1.19% 1.22% Fabricated Products and Machinery 3.25% 3.10% 3.12% Electrical Equipment 0.35% 0.51% 0.49% Automobiles and Trucks 1.66% 2.20% 2.12% Aircraft, ships, and railroad equipment 0.93% 1.25% 1.20% Precious Metals, Non-Metallic, and Industrial Metal Mining 0.25% 0.32% 0.31% Coal 0.08% 0.19% 0.17% Petroleum and Natural Gas 7.14% 5.05% 5.36% Utilities 11.62% 10.83% 10.95% Communication 5.17% 6.13% 5.99% Personal and Business Services 7.56% 8.91% 8.71% Business Equipment 4.79% 4.56% 4.60% Business Supplies and Shipping Containers 1.41% 2.24% 2.12% Transportation 3.15% 3.26% 3.24% Wholesale 3.05% 3.42% 3.37% Retail 7.77% 6.53% 6.72% Restaurants, Hotels, Motels 2.29% 2.98% 2.87% Banking, Insurance, Real Estate, Trading 17.22% 14.37% 14.80% Major industry group of comparables Unreported Reported Total Food Products 1.79% 2.85% 2.69% Beer and Liquor 0.00% 0.05% 0.05% Tobacco Products 0.00% 0.05% 0.04% Recreation 2.09% 2.39% 2.35% Printing and Publishing 1.11% 1.69% 1.60% Consumer Goods 1.19% 1.70% 1.62% Apparel 0.38% 0.68% 0.63% Healthcare, Medical Equipment, Pharmaceutical Products 5.07% 6.35% 6.15% Chemicals 2.37% 2.80% 2.73% Textiles 1.01% 0.61% 0.67% Construction and Construction Materials 5.90% 3.79% 4.11% Steel Works Etc. 1.39% 1.19% 1.22% Fabricated Products and Machinery 3.25% 3.10% 3.12% Electrical Equipment 0.35% 0.51% 0.49% Automobiles and Trucks 1.66% 2.20% 2.12% Aircraft, ships, and railroad equipment 0.93% 1.25% 1.20% Precious Metals, Non-Metallic, and Industrial Metal Mining 0.25% 0.32% 0.31% Coal 0.08% 0.19% 0.17% Petroleum and Natural Gas 7.14% 5.05% 5.36% Utilities 11.62% 10.83% 10.95% Communication 5.17% 6.13% 5.99% Personal and Business Services 7.56% 8.91% 8.71% Business Equipment 4.79% 4.56% 4.60% Business Supplies and Shipping Containers 1.41% 2.24% 2.12% Transportation 3.15% 3.26% 3.24% Wholesale 3.05% 3.42% 3.37% Retail 7.77% 6.53% 6.72% Restaurants, Hotels, Motels 2.29% 2.98% 2.87% Banking, Insurance, Real Estate, Trading 17.22% 14.37% 14.80% The table shows the industry distribution for the set of unreported and reported comparables as described in Section 2.2. Industry classification follows the Fama French 30 with the Other category omitted. Table A1 Industry distribution of unreported/reported comparables Major industry group of comparables Unreported Reported Total Food Products 1.79% 2.85% 2.69% Beer and Liquor 0.00% 0.05% 0.05% Tobacco Products 0.00% 0.05% 0.04% Recreation 2.09% 2.39% 2.35% Printing and Publishing 1.11% 1.69% 1.60% Consumer Goods 1.19% 1.70% 1.62% Apparel 0.38% 0.68% 0.63% Healthcare, Medical Equipment, Pharmaceutical Products 5.07% 6.35% 6.15% Chemicals 2.37% 2.80% 2.73% Textiles 1.01% 0.61% 0.67% Construction and Construction Materials 5.90% 3.79% 4.11% Steel Works Etc. 1.39% 1.19% 1.22% Fabricated Products and Machinery 3.25% 3.10% 3.12% Electrical Equipment 0.35% 0.51% 0.49% Automobiles and Trucks 1.66% 2.20% 2.12% Aircraft, ships, and railroad equipment 0.93% 1.25% 1.20% Precious Metals, Non-Metallic, and Industrial Metal Mining 0.25% 0.32% 0.31% Coal 0.08% 0.19% 0.17% Petroleum and Natural Gas 7.14% 5.05% 5.36% Utilities 11.62% 10.83% 10.95% Communication 5.17% 6.13% 5.99% Personal and Business Services 7.56% 8.91% 8.71% Business Equipment 4.79% 4.56% 4.60% Business Supplies and Shipping Containers 1.41% 2.24% 2.12% Transportation 3.15% 3.26% 3.24% Wholesale 3.05% 3.42% 3.37% Retail 7.77% 6.53% 6.72% Restaurants, Hotels, Motels 2.29% 2.98% 2.87% Banking, Insurance, Real Estate, Trading 17.22% 14.37% 14.80% Major industry group of comparables Unreported Reported Total Food Products 1.79% 2.85% 2.69% Beer and Liquor 0.00% 0.05% 0.05% Tobacco Products 0.00% 0.05% 0.04% Recreation 2.09% 2.39% 2.35% Printing and Publishing 1.11% 1.69% 1.60% Consumer Goods 1.19% 1.70% 1.62% Apparel 0.38% 0.68% 0.63% Healthcare, Medical Equipment, Pharmaceutical Products 5.07% 6.35% 6.15% Chemicals 2.37% 2.80% 2.73% Textiles 1.01% 0.61% 0.67% Construction and Construction Materials 5.90% 3.79% 4.11% Steel Works Etc. 1.39% 1.19% 1.22% Fabricated Products and Machinery 3.25% 3.10% 3.12% Electrical Equipment 0.35% 0.51% 0.49% Automobiles and Trucks 1.66% 2.20% 2.12% Aircraft, ships, and railroad equipment 0.93% 1.25% 1.20% Precious Metals, Non-Metallic, and Industrial Metal Mining 0.25% 0.32% 0.31% Coal 0.08% 0.19% 0.17% Petroleum and Natural Gas 7.14% 5.05% 5.36% Utilities 11.62% 10.83% 10.95% Communication 5.17% 6.13% 5.99% Personal and Business Services 7.56% 8.91% 8.71% Business Equipment 4.79% 4.56% 4.60% Business Supplies and Shipping Containers 1.41% 2.24% 2.12% Transportation 3.15% 3.26% 3.24% Wholesale 3.05% 3.42% 3.37% Retail 7.77% 6.53% 6.72% Restaurants, Hotels, Motels 2.29% 2.98% 2.87% Banking, Insurance, Real Estate, Trading 17.22% 14.37% 14.80% The table shows the industry distribution for the set of unreported and reported comparables as described in Section 2.2. Industry classification follows the Fama French 30 with the Other category omitted. Appendix B. Robustness tests In this section we present robustness tests for each of the central results of the paper. In each robustness table, we replicate a key specification from each of the main tables in the body of the paper under a variety of alternative assumptions on sample construction or regression specifications. To be conservative, in each case we choose a specification with comparable fixed effects. Table A3 replicates Column 5 of Table 2, our first main result in which we measure the causal influence of a comparable. Table A4 replicates Column 2 of Table 3, showing the growth in influence as a comparable is matched to more subsequent transactions. Table A5 replicates Column 6 of Table 4, panel B, in which we show that a comparable’s influence grows with the number of redundant paths of influence it has. In this specification, the variation in redundancy is driven only by the reported status of co-comparables, not of the comparable in question. Finally, Table A6 replicates the results from Column 4 of Table 5, in which we show that stale macroeconomic conditions are passed to new transactions through the comparable network. Table A3 Table 2 robustness tests –7 days delay +7 days delay Up to 5 comps Up to 10 comps Year-month dummies Sample weights Loan spread (1) (2) (3) (4) (5) (6) Comp Spread $$\times$$ Reported Comp 0.046** 0.041** 0.061** 0.043*** 0.050*** 0.051** (0.020) (0.018) (0.024) (0.016) (0.019) (0.022) Reported Comp –0.253** –0.222** –0.314** –0.243*** –0.262*** –0.269** (0.106) (0.091) (0.126) (0.082) (0.098) (0.114) Comp Spread $$\times$$ Precision 0.031*** 0.037*** 0.038*** 0.037*** 0.038*** 0.038*** (0.009) (0.008) (0.010) (0.008) (0.008) (0.009) Comp Precision –0.140*** –0.175*** –0.180*** –0.165*** –0.172*** –0.181*** (0.048) (0.042) (0.053) (0.039) (0.041) (0.048) Comp Spread $$\times$$ Comp Age –0.032*** –0.028*** –0.043*** –0.030*** –0.027*** –0.037*** (0.008) (0.007) (0.010) (0.006) (0.008) (0.009) Comp Age 0.170*** 0.152*** 0.224*** 0.163*** 0.139*** 0.194*** (0.044) (0.037) (0.050) (0.031) (0.043) (0.046) Comp Fixed Effects YES YES YES YES YES YES Number of Comparables 2,510 3,576 2,429 3,623 2,990 2,990 Number of Observations 14,626 20,473 11,636 25,972 17,319 17,319 $$R^2$$ 0.760 0.781 0.784 0.764 0.789 0.806 –7 days delay +7 days delay Up to 5 comps Up to 10 comps Year-month dummies Sample weights Loan spread (1) (2) (3) (4) (5) (6) Comp Spread $$\times$$ Reported Comp 0.046** 0.041** 0.061** 0.043*** 0.050*** 0.051** (0.020) (0.018) (0.024) (0.016) (0.019) (0.022) Reported Comp –0.253** –0.222** –0.314** –0.243*** –0.262*** –0.269** (0.106) (0.091) (0.126) (0.082) (0.098) (0.114) Comp Spread $$\times$$ Precision 0.031*** 0.037*** 0.038*** 0.037*** 0.038*** 0.038*** (0.009) (0.008) (0.010) (0.008) (0.008) (0.009) Comp Precision –0.140*** –0.175*** –0.180*** –0.165*** –0.172*** –0.181*** (0.048) (0.042) (0.053) (0.039) (0.041) (0.048) Comp Spread $$\times$$ Comp Age –0.032*** –0.028*** –0.043*** –0.030*** –0.027*** –0.037*** (0.008) (0.007) (0.010) (0.006) (0.008) (0.009) Comp Age 0.170*** 0.152*** 0.224*** 0.163*** 0.139*** 0.194*** (0.044) (0.037) (0.050) (0.031) (0.043) (0.046) Comp Fixed Effects YES YES YES YES YES YES Number of Comparables 2,510 3,576 2,429 3,623 2,990 2,990 Number of Observations 14,626 20,473 11,636 25,972 17,319 17,319 $$R^2$$ 0.760 0.781 0.784 0.764 0.789 0.806 The table estimates Column 6 of Table 2 under a variety of alternative assumptions. The main variable of interest is $$Comp Spread \times Reported Comp$$, which captures the causal influence of a comparable’s interest rate spread on spreads of subsequent, similar transactions. In Column 1, we assume that all loans were reported seven days earlier than in the baseline results. In Column 2, we assume they were reported seven days later. Column 3 limits the maximum number of comparables per transaction to five (relative to seven in the baseline results), while Column 4 allows up to ten. Columns 5 and 6 use the same sample as in the baseline results but vary the regression specification. Column 5 includes calendar year-month dummies as of the closing month of the new transaction being priced. Column 6 imposes sample weights that give each comparable equal influence in the regression. Standard errors are reported in parentheses and are clustered at the level of comparable firm and borrowing firm. ***, **, and * indicate significance at the 1%, 5%, and 10% levels, respectively. Table A3 Table 2 robustness tests –7 days delay +7 days delay Up to 5 comps Up to 10 comps Year-month dummies Sample weights Loan spread (1) (2) (3) (4) (5) (6) Comp Spread $$\times$$ Reported Comp 0.046** 0.041** 0.061** 0.043*** 0.050*** 0.051** (0.020) (0.018) (0.024) (0.016) (0.019) (0.022) Reported Comp –0.253** –0.222** –0.314** –0.243*** –0.262*** –0.269** (0.106) (0.091) (0.126) (0.082) (0.098) (0.114) Comp Spread $$\times$$ Precision 0.031*** 0.037*** 0.038*** 0.037*** 0.038*** 0.038*** (0.009) (0.008) (0.010) (0.008) (0.008) (0.009) Comp Precision –0.140*** –0.175*** –0.180*** –0.165*** –0.172*** –0.181*** (0.048) (0.042) (0.053) (0.039) (0.041) (0.048) Comp Spread $$\times$$ Comp Age –0.032*** –0.028*** –0.043*** –0.030*** –0.027*** –0.037*** (0.008) (0.007) (0.010) (0.006) (0.008) (0.009) Comp Age 0.170*** 0.152*** 0.224*** 0.163*** 0.139*** 0.194*** (0.044) (0.037) (0.050) (0.031) (0.043) (0.046) Comp Fixed Effects YES YES YES YES YES YES Number of Comparables 2,510 3,576 2,429 3,623 2,990 2,990 Number of Observations 14,626 20,473 11,636 25,972 17,319 17,319 $$R^2$$ 0.760 0.781 0.784 0.764 0.789 0.806 –7 days delay +7 days delay Up to 5 comps Up to 10 comps Year-month dummies Sample weights Loan spread (1) (2) (3) (4) (5) (6) Comp Spread $$\times$$ Reported Comp 0.046** 0.041** 0.061** 0.043*** 0.050*** 0.051** (0.020) (0.018) (0.024) (0.016) (0.019) (0.022) Reported Comp –0.253** –0.222** –0.314** –0.243*** –0.262*** –0.269** (0.106) (0.091) (0.126) (0.082) (0.098) (0.114) Comp Spread $$\times$$ Precision 0.031*** 0.037*** 0.038*** 0.037*** 0.038*** 0.038*** (0.009) (0.008) (0.010) (0.008) (0.008) (0.009) Comp Precision –0.140*** –0.175*** –0.180*** –0.165*** –0.172*** –0.181*** (0.048) (0.042) (0.053) (0.039) (0.041) (0.048) Comp Spread $$\times$$ Comp Age –0.032*** –0.028*** –0.043*** –0.030*** –0.027*** –0.037*** (0.008) (0.007) (0.010) (0.006) (0.008) (0.009) Comp Age 0.170*** 0.152*** 0.224*** 0.163*** 0.139*** 0.194*** (0.044) (0.037) (0.050) (0.031) (0.043) (0.046) Comp Fixed Effects YES YES YES YES YES YES Number of Comparables 2,510 3,576 2,429 3,623 2,990 2,990 Number of Observations 14,626 20,473 11,636 25,972 17,319 17,319 $$R^2$$ 0.760 0.781 0.784 0.764 0.789 0.806 The table estimates Column 6 of Table 2 under a variety of alternative assumptions. The main variable of interest is $$Comp Spread \times Reported Comp$$, which captures the causal influence of a comparable’s interest rate spread on spreads of subsequent, similar transactions. In Column 1, we assume that all loans were reported seven days earlier than in the baseline results. In Column 2, we assume they were reported seven days later. Column 3 limits the maximum number of comparables per transaction to five (relative to seven in the baseline results), while Column 4 allows up to ten. Columns 5 and 6 use the same sample as in the baseline results but vary the regression specification. Column 5 includes calendar year-month dummies as of the closing month of the new transaction being priced. Column 6 imposes sample weights that give each comparable equal influence in the regression. Standard errors are reported in parentheses and are clustered at the level of comparable firm and borrowing firm. ***, **, and * indicate significance at the 1%, 5%, and 10% levels, respectively. Table A4 Table 3 robustness tests –7 days delay +7 days delay Up to 5 comps Up to 10 comps Year-month dummies Sample weights Loan spread (1) (2) (3) (4) (5) (6) Comp Spread $$\times$$ 2nd –0.020 –0.016 –0.006 –0.005 –0.022 –0.028 $$\quad$$ Match (Unreported) (0.026) (0.021) (0.027) (0.020) (0.022) (0.025) Comp Spread $$\times$$$$\geq$$ 3rd –0.018 0.003 0.011 0.001 –0.009 –0.019 $$\quad$$ Match (Unreported) (0.029) (0.025) (0.032) (0.023) (0.025) (0.030) Comp Spread $$\times$$ 1st 0.049* 0.050** 0.079*** 0.054** 0.063*** 0.052* $$\quad$$ Match (Reported)a (0.026) (0.023) (0.029) (0.022) (0.024) (0.029) Comp Spread $$\times$$ 2nd 0.068** 0.070*** 0.088** 0.067** 0.069** 0.050 $$\quad$$ Match (Reported) (0.033) (0.027) (0.037) (0.027) (0.029) (0.034) Comp Spread $$\times$$ 3rd 0.100*** 0.064* 0.110*** 0.079*** 0.103*** 0.084** $$\quad$$ Match (Reported) (0.036) (0.033) (0.041) (0.029) (0.032) (0.038) Comp Spread $$\times$$ 4th 0.133*** 0.096*** 0.134*** 0.110*** 0.117*** 0.109** $$\quad$$ Match (Reported) (0.042) (0.036) (0.046) (0.032) (0.036) (0.046) Comp Spread $$\times$$$$\geq$$ 5th 0.126*** 0.099*** 0.120*** 0.137*** 0.117** $$\quad$$ Match (Reported)b (0.046) (0.038) (0.036) (0.039) (0.048) (b)–(a) 0.077** 0.049** 0.055* 0.066*** 0.074*** 0.065** Other Controls YES YES YES YES YES YES Comp Fixed Effects YES YES YES YES YES YES Number of Comparables 2,510 3,576 2,429 3,623 2,990 2,990 Number of Observations 14,626 20,473 11,636 25,972 17,319 17,319 $$R^2$$ 0.761 0.782 0.785 0.765 0.790 0.807 –7 days delay +7 days delay Up to 5 comps Up to 10 comps Year-month dummies Sample weights Loan spread (1) (2) (3) (4) (5) (6) Comp Spread $$\times$$ 2nd –0.020 –0.016 –0.006 –0.005 –0.022 –0.028 $$\quad$$ Match (Unreported) (0.026) (0.021) (0.027) (0.020) (0.022) (0.025) Comp Spread $$\times$$$$\geq$$ 3rd –0.018 0.003 0.011 0.001 –0.009 –0.019 $$\quad$$ Match (Unreported) (0.029) (0.025) (0.032) (0.023) (0.025) (0.030) Comp Spread $$\times$$ 1st 0.049* 0.050** 0.079*** 0.054** 0.063*** 0.052* $$\quad$$ Match (Reported)a (0.026) (0.023) (0.029) (0.022) (0.024) (0.029) Comp Spread $$\times$$ 2nd 0.068** 0.070*** 0.088** 0.067** 0.069** 0.050 $$\quad$$ Match (Reported) (0.033) (0.027) (0.037) (0.027) (0.029) (0.034) Comp Spread $$\times$$ 3rd 0.100*** 0.064* 0.110*** 0.079*** 0.103*** 0.084** $$\quad$$ Match (Reported) (0.036) (0.033) (0.041) (0.029) (0.032) (0.038) Comp Spread $$\times$$ 4th 0.133*** 0.096*** 0.134*** 0.110*** 0.117*** 0.109** $$\quad$$ Match (Reported) (0.042) (0.036) (0.046) (0.032) (0.036) (0.046) Comp Spread $$\times$$$$\geq$$ 5th 0.126*** 0.099*** 0.120*** 0.137*** 0.117** $$\quad$$ Match (Reported)b (0.046) (0.038) (0.036) (0.039) (0.048) (b)–(a) 0.077** 0.049** 0.055* 0.066*** 0.074*** 0.065** Other Controls YES YES YES YES YES YES Comp Fixed Effects YES YES YES YES YES YES Number of Comparables 2,510 3,576 2,429 3,623 2,990 2,990 Number of Observations 14,626 20,473 11,636 25,972 17,319 17,319 $$R^2$$ 0.761 0.782 0.785 0.765 0.790 0.807 The table estimates Column 2 of Table 3 under a variety of alternative assumptions. The pattern of interest is the growth in influence with additional comparable matches after the comparable is reported. In Column 1, we assume that all loans were reported seven days earlier than in the baseline results. In Column 2, we assume they were reported seven days later. Column 3 limits the maximum number of comparables per transaction to five (relative to seven in the baseline results). Because this results in few comparables with five or more matches, the last dummy in this column is for four or more matches. The test for growth in influence (reported as (b)–(a)) is modified accordingly. Column 4 allows up to ten comparables per transaction. Columns 5 and 6 use the same sample as in the baseline results but vary the regression specification. Column 5 includes calendar year-month dummies as of the closing month of the new transaction being priced. Column 6 imposes sample weights that give each comparable equal influence in the regression. Standard errors are reported in parentheses and are clustered at the level of comparable firm and borrowing firm. ***, **, and * indicate significance at the 1%, 5%, and 10% levels, respectively. Table A4 Table 3 robustness tests –7 days delay +7 days delay Up to 5 comps Up to 10 comps Year-month dummies Sample weights Loan spread (1) (2) (3) (4) (5) (6) Comp Spread $$\times$$ 2nd –0.020 –0.016 –0.006 –0.005 –0.022 –0.028 $$\quad$$ Match (Unreported) (0.026) (0.021) (0.027) (0.020) (0.022) (0.025) Comp Spread $$\times$$$$\geq$$ 3rd –0.018 0.003 0.011 0.001 –0.009 –0.019 $$\quad$$ Match (Unreported) (0.029) (0.025) (0.032) (0.023) (0.025) (0.030) Comp Spread $$\times$$ 1st 0.049* 0.050** 0.079*** 0.054** 0.063*** 0.052* $$\quad$$ Match (Reported)a (0.026) (0.023) (0.029) (0.022) (0.024) (0.029) Comp Spread $$\times$$ 2nd 0.068** 0.070*** 0.088** 0.067** 0.069** 0.050 $$\quad$$ Match (Reported) (0.033) (0.027) (0.037) (0.027) (0.029) (0.034) Comp Spread $$\times$$ 3rd 0.100*** 0.064* 0.110*** 0.079*** 0.103*** 0.084** $$\quad$$ Match (Reported) (0.036) (0.033) (0.041) (0.029) (0.032) (0.038) Comp Spread $$\times$$ 4th 0.133*** 0.096*** 0.134*** 0.110*** 0.117*** 0.109** $$\quad$$ Match (Reported) (0.042) (0.036) (0.046) (0.032) (0.036) (0.046) Comp Spread $$\times$$$$\geq$$ 5th 0.126*** 0.099*** 0.120*** 0.137*** 0.117** $$\quad$$ Match (Reported)b (0.046) (0.038) (0.036) (0.039) (0.048) (b)–(a) 0.077** 0.049** 0.055* 0.066*** 0.074*** 0.065** Other Controls YES YES YES YES YES YES Comp Fixed Effects YES YES YES YES YES YES Number of Comparables 2,510 3,576 2,429 3,623 2,990 2,990 Number of Observations 14,626 20,473 11,636 25,972 17,319 17,319 $$R^2$$ 0.761 0.782 0.785 0.765 0.790 0.807 –7 days delay +7 days delay Up to 5 comps Up to 10 comps Year-month dummies Sample weights Loan spread (1) (2) (3) (4) (5) (6) Comp Spread $$\times$$ 2nd –0.020 –0.016 –0.006 –0.005 –0.022 –0.028 $$\quad$$ Match (Unreported) (0.026) (0.021) (0.027) (0.020) (0.022) (0.025) Comp Spread $$\times$$$$\geq$$ 3rd –0.018 0.003 0.011 0.001 –0.009 –0.019 $$\quad$$ Match (Unreported) (0.029) (0.025) (0.032) (0.023) (0.025) (0.030) Comp Spread $$\times$$ 1st 0.049* 0.050** 0.079*** 0.054** 0.063*** 0.052* $$\quad$$ Match (Reported)a (0.026) (0.023) (0.029) (0.022) (0.024) (0.029) Comp Spread $$\times$$ 2nd 0.068** 0.070*** 0.088** 0.067** 0.069** 0.050 $$\quad$$ Match (Reported) (0.033) (0.027) (0.037) (0.027) (0.029) (0.034) Comp Spread $$\times$$ 3rd 0.100*** 0.064* 0.110*** 0.079*** 0.103*** 0.084** $$\quad$$ Match (Reported) (0.036) (0.033) (0.041) (0.029) (0.032) (0.038) Comp Spread $$\times$$ 4th 0.133*** 0.096*** 0.134*** 0.110*** 0.117*** 0.109** $$\quad$$ Match (Reported) (0.042) (0.036) (0.046) (0.032) (0.036) (0.046) Comp Spread $$\times$$$$\geq$$ 5th 0.126*** 0.099*** 0.120*** 0.137*** 0.117** $$\quad$$ Match (Reported)b (0.046) (0.038) (0.036) (0.039) (0.048) (b)–(a) 0.077** 0.049** 0.055* 0.066*** 0.074*** 0.065** Other Controls YES YES YES YES YES YES Comp Fixed Effects YES YES YES YES YES YES Number of Comparables 2,510 3,576 2,429 3,623 2,990 2,990 Number of Observations 14,626 20,473 11,636 25,972 17,319 17,319 $$R^2$$ 0.761 0.782 0.785 0.765 0.790 0.807 The table estimates Column 2 of Table 3 under a variety of alternative assumptions. The pattern of interest is the growth in influence with additional comparable matches after the comparable is reported. In Column 1, we assume that all loans were reported seven days earlier than in the baseline results. In Column 2, we assume they were reported seven days later. Column 3 limits the maximum number of comparables per transaction to five (relative to seven in the baseline results). Because this results in few comparables with five or more matches, the last dummy in this column is for four or more matches. The test for growth in influence (reported as (b)–(a)) is modified accordingly. Column 4 allows up to ten comparables per transaction. Columns 5 and 6 use the same sample as in the baseline results but vary the regression specification. Column 5 includes calendar year-month dummies as of the closing month of the new transaction being priced. Column 6 imposes sample weights that give each comparable equal influence in the regression. Standard errors are reported in parentheses and are clustered at the level of comparable firm and borrowing firm. ***, **, and * indicate significance at the 1%, 5%, and 10% levels, respectively. Table A5 Table 4 robustness tests –7 days delay +7 days delay Up to 5 comps Up to 10 comps Year-month dummies Sample weights Loan spread (1) (2) (3) (4) (5) (6) Comp Spread $$\times$$ 1 0.030 0.022 0.038** 0.018 0.027 0.007 $$\quad$$ Redundancya (0.019) (0.015) (0.017) (0.018) (0.017) (0.019) Comp Spread $$\times$$ 2 0.051** 0.038* 0.057** 0.009 0.054*** 0.047** $$\quad$$ Redundancies (0.022) (0.020) (0.024) (0.018) (0.020) (0.022) Comp Spread $$\times$$ 3 0.094*** 0.062*** 0.069** 0.032 0.089*** 0.081*** $$\quad$$ Redundancies (0.027) (0.023) (0.030) (0.021) (0.025) (0.026) Comp Spread $$\times$$$$\geq$$ 4 0.105*** 0.073*** 0.067*** 0.111*** 0.094*** $$\quad$$ Redundanciesb (0.030) (0.027) (0.025) (0.029) (0.030) (b)–(a) 0.075*** 0.051** 0.031 0.049** 0.084*** 0.087*** Other Controls YES YES YES YES YES YES Comp Fixed Effects YES YES YES YES YES YES Number of Comparables 2,953 4,245 2,814 4,157 3,569 3,569 Observations 14,500 20,107 10,815 25,170 17,188 17,188 $$R^2$$ 0.826 0.841 0.855 0.814 0.856 0.863 –7 days delay +7 days delay Up to 5 comps Up to 10 comps Year-month dummies Sample weights Loan spread (1) (2) (3) (4) (5) (6) Comp Spread $$\times$$ 1 0.030 0.022 0.038** 0.018 0.027 0.007 $$\quad$$ Redundancya (0.019) (0.015) (0.017) (0.018) (0.017) (0.019) Comp Spread $$\times$$ 2 0.051** 0.038* 0.057** 0.009 0.054*** 0.047** $$\quad$$ Redundancies (0.022) (0.020) (0.024) (0.018) (0.020) (0.022) Comp Spread $$\times$$ 3 0.094*** 0.062*** 0.069** 0.032 0.089*** 0.081*** $$\quad$$ Redundancies (0.027) (0.023) (0.030) (0.021) (0.025) (0.026) Comp Spread $$\times$$$$\geq$$ 4 0.105*** 0.073*** 0.067*** 0.111*** 0.094*** $$\quad$$ Redundanciesb (0.030) (0.027) (0.025) (0.029) (0.030) (b)–(a) 0.075*** 0.051** 0.031 0.049** 0.084*** 0.087*** Other Controls YES YES YES YES YES YES Comp Fixed Effects YES YES YES YES YES YES Number of Comparables 2,953 4,245 2,814 4,157 3,569 3,569 Observations 14,500 20,107 10,815 25,170 17,188 17,188 $$R^2$$ 0.826 0.841 0.855 0.814 0.856 0.863 The table estimates Column 6 of Table 4, panel B under a variety of alternative assumptions. Of interest is the growth in influence with additional paths of redundancy, as well as the simple fact that redundant comparables are more influential (nonredundant comparables are the omitted category). In Column 1, we assume that all loans were reported seven days earlier than in the baseline results. In Column 2, we assume they were reported seven days later. Column 3 limits the maximum number of comparables per transaction to five (relative to seven in the baseline results). Because this results in few comparables with four or more redundancies, the last dummy in this column is for three or more redundancies. The test for growth in influence (reported as (b)–(a)) is modified accordingly. Column 4 allows up to ten comparables per transaction. Columns 5 and 6 use the same sample as in the baseline results but vary the regression specification. Column 5 includes calendar year-month dummies as of the closing month of the new transaction being priced. Column 6 imposes sample weights that give each comparable equal influence in the regression. Standard errors are reported in parentheses and are clustered at the level of comparable firm and borrowing firm. ***, **, and * indicate significance at the 1%, 5%, and 10% levels, respectively. Table A5 Table 4 robustness tests –7 days delay +7 days delay Up to 5 comps Up to 10 comps Year-month dummies Sample weights Loan spread (1) (2) (3) (4) (5) (6) Comp Spread $$\times$$ 1 0.030 0.022 0.038** 0.018 0.027 0.007 $$\quad$$ Redundancya (0.019) (0.015) (0.017) (0.018) (0.017) (0.019) Comp Spread $$\times$$ 2 0.051** 0.038* 0.057** 0.009 0.054*** 0.047** $$\quad$$ Redundancies (0.022) (0.020) (0.024) (0.018) (0.020) (0.022) Comp Spread $$\times$$ 3 0.094*** 0.062*** 0.069** 0.032 0.089*** 0.081*** $$\quad$$ Redundancies (0.027) (0.023) (0.030) (0.021) (0.025) (0.026) Comp Spread $$\times$$$$\geq$$ 4 0.105*** 0.073*** 0.067*** 0.111*** 0.094*** $$\quad$$ Redundanciesb (0.030) (0.027) (0.025) (0.029) (0.030) (b)–(a) 0.075*** 0.051** 0.031 0.049** 0.084*** 0.087*** Other Controls YES YES YES YES YES YES Comp Fixed Effects YES YES YES YES YES YES Number of Comparables 2,953 4,245 2,814 4,157 3,569 3,569 Observations 14,500 20,107 10,815 25,170 17,188 17,188 $$R^2$$ 0.826 0.841 0.855 0.814 0.856 0.863 –7 days delay +7 days delay Up to 5 comps Up to 10 comps Year-month dummies Sample weights Loan spread (1) (2) (3) (4) (5) (6) Comp Spread $$\times$$ 1 0.030 0.022 0.038** 0.018 0.027 0.007 $$\quad$$ Redundancya (0.019) (0.015) (0.017) (0.018) (0.017) (0.019) Comp Spread $$\times$$ 2 0.051** 0.038* 0.057** 0.009 0.054*** 0.047** $$\quad$$ Redundancies (0.022) (0.020) (0.024) (0.018) (0.020) (0.022) Comp Spread $$\times$$ 3 0.094*** 0.062*** 0.069** 0.032 0.089*** 0.081*** $$\quad$$ Redundancies (0.027) (0.023) (0.030) (0.021) (0.025) (0.026) Comp Spread $$\times$$$$\geq$$ 4 0.105*** 0.073*** 0.067*** 0.111*** 0.094*** $$\quad$$ Redundanciesb (0.030) (0.027) (0.025) (0.029) (0.030) (b)–(a) 0.075*** 0.051** 0.031 0.049** 0.084*** 0.087*** Other Controls YES YES YES YES YES YES Comp Fixed Effects YES YES YES YES YES YES Number of Comparables 2,953 4,245 2,814 4,157 3,569 3,569 Observations 14,500 20,107 10,815 25,170 17,188 17,188 $$R^2$$ 0.826 0.841 0.855 0.814 0.856 0.863 The table estimates Column 6 of Table 4, panel B under a variety of alternative assumptions. Of interest is the growth in influence with additional paths of redundancy, as well as the simple fact that redundant comparables are more influential (nonredundant comparables are the omitted category). In Column 1, we assume that all loans were reported seven days earlier than in the baseline results. In Column 2, we assume they were reported seven days later. Column 3 limits the maximum number of comparables per transaction to five (relative to seven in the baseline results). Because this results in few comparables with four or more redundancies, the last dummy in this column is for three or more redundancies. The test for growth in influence (reported as (b)–(a)) is modified accordingly. Column 4 allows up to ten comparables per transaction. Columns 5 and 6 use the same sample as in the baseline results but vary the regression specification. Column 5 includes calendar year-month dummies as of the closing month of the new transaction being priced. Column 6 imposes sample weights that give each comparable equal influence in the regression. Standard errors are reported in parentheses and are clustered at the level of comparable firm and borrowing firm. ***, **, and * indicate significance at the 1%, 5%, and 10% levels, respectively. Table A6 Table 5 robustness tests Panel A: First stage –7 days delay +7 days delay Up to 5 comps Up to 10 comps Average Comp Spread (1) (2) (3) (4) 0.113** 0.106** 0.125*** 0.109** $$\overline{\text{Baa-Aaa Spread}}$$ (at comp closing) (0.048) (0.047) (0.045) (0.052) 13.743** 13.665** 13.649** 12.940* $$\overline{\text{Market D/P}}$$ (at comp closing) (6.887) (6.924) (6.600) (7.278) 0.753*** 0.712*** 0.647*** 0.812*** $$\overline{\text{VIX}}$$ (at comp closing) (0.182) (0.180) (0.166) (0.196) $$R^2$$ 0.825 0.824 0.820 0.825 F-statistic (excluded instruments) 23.17 20.97 19.50 21.29 p-value of F-statistic 0.00 0.00 0.00 0.00 Panel B: Second stage Loan spread (1) (2) (3) (4) Average Comp Spread 0.550*** 0.601*** 0.447*** 0.590*** (0.142) (0.143) (0.131) (0.139) Year $$\times$$ Month Fixed Effects YES YES YES YES Rating and Industry Fixed Effects YES YES YES YES Loan Controls YES YES YES YES Number of Months 299 299 299 300 Number of Observations 25,408 25,333 25,364 25,377 Panel A: First stage –7 days delay +7 days delay Up to 5 comps Up to 10 comps Average Comp Spread (1) (2) (3) (4) 0.113** 0.106** 0.125*** 0.109** $$\overline{\text{Baa-Aaa Spread}}$$ (at comp closing) (0.048) (0.047) (0.045) (0.052) 13.743** 13.665** 13.649** 12.940* $$\overline{\text{Market D/P}}$$ (at comp closing) (6.887) (6.924) (6.600) (7.278) 0.753*** 0.712*** 0.647*** 0.812*** $$\overline{\text{VIX}}$$ (at comp closing) (0.182) (0.180) (0.166) (0.196) $$R^2$$ 0.825 0.824 0.820 0.825 F-statistic (excluded instruments) 23.17 20.97 19.50 21.29 p-value of F-statistic 0.00 0.00 0.00 0.00 Panel B: Second stage Loan spread (1) (2) (3) (4) Average Comp Spread 0.550*** 0.601*** 0.447*** 0.590*** (0.142) (0.143) (0.131) (0.139) Year $$\times$$ Month Fixed Effects YES YES YES YES Rating and Industry Fixed Effects YES YES YES YES Loan Controls YES YES YES YES Number of Months 299 299 299 300 Number of Observations 25,408 25,333 25,364 25,377 The table estimates Column 4 of Table 5 under a variety of alternative assumptions. Using 2SLS to track the path of influence, the table shows that stale macroeconomic conditions affect the at-issue interest rate spreads of new transactions through the use of comparables. In Column 1, we assume that all loans were reported seven days earlier than in the baseline results. In Column 2, we assume they were reported seven days later. Column 3 limits the maximum number of comparables per transaction to five (relative to seven in the baseline results), while Column 4 allows up to ten comparables per transaction. Standard errors are reported in parentheses and are clustered at the level of the borrowing firm and month. ***, **, and * indicate significance at the 1%, 5%, and 10% levels, respectively. Table A6 Table 5 robustness tests Panel A: First stage –7 days delay +7 days delay Up to 5 comps Up to 10 comps Average Comp Spread (1) (2) (3) (4) 0.113** 0.106** 0.125*** 0.109** $$\overline{\text{Baa-Aaa Spread}}$$ (at comp closing) (0.048) (0.047) (0.045) (0.052) 13.743** 13.665** 13.649** 12.940* $$\overline{\text{Market D/P}}$$ (at comp closing) (6.887) (6.924) (6.600) (7.278) 0.753*** 0.712*** 0.647*** 0.812*** $$\overline{\text{VIX}}$$ (at comp closing) (0.182) (0.180) (0.166) (0.196) $$R^2$$ 0.825 0.824 0.820 0.825 F-statistic (excluded instruments) 23.17 20.97 19.50 21.29 p-value of F-statistic 0.00 0.00 0.00 0.00 Panel B: Second stage Loan spread (1) (2) (3) (4) Average Comp Spread 0.550*** 0.601*** 0.447*** 0.590*** (0.142) (0.143) (0.131) (0.139) Year $$\times$$ Month Fixed Effects YES YES YES YES Rating and Industry Fixed Effects YES YES YES YES Loan Controls YES YES YES YES Number of Months 299 299 299 300 Number of Observations 25,408 25,333 25,364 25,377 Panel A: First stage –7 days delay +7 days delay Up to 5 comps Up to 10 comps Average Comp Spread (1) (2) (3) (4) 0.113** 0.106** 0.125*** 0.109** $$\overline{\text{Baa-Aaa Spread}}$$ (at comp closing) (0.048) (0.047) (0.045) (0.052) 13.743** 13.665** 13.649** 12.940* $$\overline{\text{Market D/P}}$$ (at comp closing) (6.887) (6.924) (6.600) (7.278) 0.753*** 0.712*** 0.647*** 0.812*** $$\overline{\text{VIX}}$$ (at comp closing) (0.182) (0.180) (0.166) (0.196) $$R^2$$ 0.825 0.824 0.820 0.825 F-statistic (excluded instruments) 23.17 20.97 19.50 21.29 p-value of F-statistic 0.00 0.00 0.00 0.00 Panel B: Second stage Loan spread (1) (2) (3) (4) Average Comp Spread 0.550*** 0.601*** 0.447*** 0.590*** (0.142) (0.143) (0.131) (0.139) Year $$\times$$ Month Fixed Effects YES YES YES YES Rating and Industry Fixed Effects YES YES YES YES Loan Controls YES YES YES YES Number of Months 299 299 299 300 Number of Observations 25,408 25,333 25,364 25,377 The table estimates Column 4 of Table 5 under a variety of alternative assumptions. Using 2SLS to track the path of influence, the table shows that stale macroeconomic conditions affect the at-issue interest rate spreads of new transactions through the use of comparables. In Column 1, we assume that all loans were reported seven days earlier than in the baseline results. In Column 2, we assume they were reported seven days later. Column 3 limits the maximum number of comparables per transaction to five (relative to seven in the baseline results), while Column 4 allows up to ten comparables per transaction. Standard errors are reported in parentheses and are clustered at the level of the borrowing firm and month. ***, **, and * indicate significance at the 1%, 5%, and 10% levels, respectively. The first step in our analysis was to recover reporting dates for each loan based on the loan’s PackageID. As described in Section 2.1, we estimate relative loan report dates based on the sequential nature of PackageID. To pin down the absolute date, we set the median reporting delay to 14 days as of the last full year for which we have data, based on claims by the data provider that “the majority of transactions” are reported within two weeks. In the tables that follow, the first two Columns test the sensitivity of our results to this assumption by perturbing all reporting dates to be seven days earlier (Columns 1) or seven days later (Columns 2). In each case, we re-run our comparable matching procedure and sample selection criteria described in Section 2.2. Recall that throughout the paper we condition on comparables that match to at least one subsequent transaction both before and after being reported. Because perturbing the report date changes the reported status of some comparables for some matched transactions, the number of observations in our sample changes predictably. For example, in Column 1 we have assumed that transactions are reported seven days earlier than in the baseline results. This results in fewer unreported comparables and, hence, a smaller sample size. Thus, Columns 1 and 2 effectively test the robustness of our results both to changes in assumed reporting dates and to somewhat different samples. The same is true for Columns 3 and 4, in which we examine perturbations to the maximum number of comparables that we assume any transaction can have. In the baseline results, we set the upper bound to seven so as to give each transaction an average of five reported comparables. In Columns 3 and 4 of the robustness tables, we set the maximum number of comparables per transaction to five and ten, respectively. Of course, this results in fewer comparables per transaction on average in Column 3. Consequently, for Tables A4 and A5, which feature dummies for the number of comparable matches or the number of redundancies, we truncate the maximum number at one fewer than in the baseline results. Columns 5 and 6 work with identical samples as in their corresponding baseline results but examine the robustness of our results to alternative regression specifications. In Column 5 we add calendar year-month dummies as of the closing month of the new transaction being priced to soak up any variation over time that might be behind our results. A significant amount of this variation is, of course, already absorbed by the comparable fixed effects included in many of the baseline results and all of the robustness tests. Column 6 imposes sample weights on the data such that each comparable is given equal influence in the regression. This ensures that our results are not being driven by a small number of highly influential comparables. In all cases, our results are robust to the alternative assumptions or specifications, with the lone exception of Column 3 of Table A5 in which we measure the growth in influence of a comparable with increasing paths of redundancy under the assumption that each new transaction can match to a maximum of five comparables. As mentioned above, with fewer matches per comparable, we truncate the number of redundancies at a maximum of three (as opposed to four for all other specifications). While the point estimate grows with the each additional path of redundancy, the influence of a comparable with three or more redundancies is not statistically significantly different from the influence of a comparable with one. That said, the most basic takeaway from Table 4—that redundant comparables are more influential than nonredundant comparables—is still readily apparent. Footnotes 1 Recent work by Eyster and Rabin (2010, 2014) shows that in many cases, efficient observational learning in the presence of overlapping information requires agents to “anti-imitate” the actions of past agents. In a comparables framework, this means that for a particularly influential comparable, a higher observed price on the comparable can imply a lower optimal price on the transaction it informs, ceteris paribus. We give examples of this surprising result in the next section. 2 An important step in our analysis is the matching of new loans to their likely comparables. We discuss our matching process in detail in Section 2, but, briefly, we do our best to replicate a natural search procedure an analyst might perform when combing a database for comparables: search by industry and loan type, then look for similarly rated borrowers within that cohort. In the Appendix we explore the robustness of our results to variation in matching rules. 3 Call the variance of the prior period’s best estimate of fundamentals $${\sigma}^2_{t-1}$$; then $$w_t = \frac{{\sigma}^2_u}{{\sigma}^2_u + \rho^2 {\sigma}^2_{t-1} + {\sigma}^2_v}$$. 4 If, for example, multiple agents price multiple transactions each period or if past transactions are observed with delay, using multiple comparables is optimal (Eyster and Rabin 2014). 5 We could imagine other naïve approaches to comparables pricing. For example, the agent may equal-weight signal D and transactions B and C, realizing that the transactions at time 2 nest transaction A. In any case, so long as he fails to negatively weight transaction A, he neglects the redundancy in his information set, resulting in the same empirical patterns. 6 To see this clearly, consider the Kalman filter proposed in Equation (3). A regression of current prices on past prices, $$p_t=\beta p_{t-1}+\epsilon_t$$, yields a coefficient on $$p_{t-1}$$ given by $$\hat{\beta}=w\rho+(1-w)\hat{\beta}_{s,p_{t-1}}$$, where $$\hat{\beta}_{s,p_{t-1}}$$ is the coefficient in a univariate regression of $$s_t$$ on $$p_{t-1}$$. The first term captures the causal impact of the comparable, whereas the second term represents a bias due to the confounding relationship between $$p_{t-1}$$ and $$s_t$$. 7 One widely used lending manual advises that “a syndication department will use all types of market intelligence to assist in forming its view of the appropriate structure and price for a particular deal.... This usually involves identifying transactions that have been arranged for broadly comparable borrowers” (Rhodes 2008). The Loan Syndication and Trading Association’s guide to the primary and secondary loan market suggests that among the primary factors to be considered when setting interest rates for a borrower are the set of “comparable prior transactions (i.e. similar industry, use of proceeds, size and company and so on)” (Taylor and Sansone 2006). 8 Generally, a lead arranger, or perhaps a small group of lead arrangers, will propose deal pricing to a borrower in a competitive bidding process prior to receiving a formal mandate. After receiving the mandate, the loan will be syndicated to participant banks at the proposed interest rate. Over time, parts of the loan market have converged closer to a model of bond pricing, whereby lenders set indicative pricing, but then terms are “flexed” during syndication to meet investor demand. In this case, the influence of comparables on the actual loan interest rate will manifest by way of the lead bank’s initial indicative pricing, as well as through investors’ use of comparables. 9 The methodology for uncovering reporting dates, which are implicitly but not explicitly shared by the data provider, depends on the fact that loans are assigned a unique identifier upon entry into the database, and that unique identifier is serial in nature, providing a ranking of transactions based on reporting dates that is not perfectly aligned with closing dates. We discuss this later in greater detail. 10 In general, we believe that an imperfect classification of known versus unknown comparables will bias our main estimates toward zero. Thus, it may be appropriate to think of the economic magnitudes at play as being lower bounds on the true magnitudes. 11 In the robustness tables in the Appendix, we show that none of our main results depend importantly on this choice. 12 We exclude non-U.S. transactions in the estimation of this curve and have made adjustments for the acquisition of an Asian debt market data provider in 2000, which, in the raw data, was related to a gap of roughly 33,000 in the sequence of PackageIDs. 13 So, for example, the distance between a rating of BBB and BB would be three, where BBB- and BB+ are the intervening categories. 14 Meanwhile, Griliches and Hausman (1986) (among others) show that the inclusion of fixed effects may mechanically amplify attenuation bias due to measurement error, in particular when the error is negatively autocorrelated within a cross-sectional unit, as is likely the case in our setting. 15 This follows from noting the summation of the pricing errors is a geometric series. 16 Note that, as suggested by Figure 5, the control for $$CompAge \times CompSpread$$ is important here. Without it, the expected decrease in influence due to the passage of time offsets the increased influence due to repeated comparable use. 17 Of course, the path of redundancy would also be closed in the case that A was not reported in time for B$$'$$ and B$$'$$ was not reported in time for C$$'$$. This case is included among the nonredundant observations in our regressions in panel A of Table 4 but was omitted from Figure 7 for ease of exposition. 18 The two implicit first-stage regressions are omitted in the main text for brevity, but included in Table A2 of the Appendix. Not surprisingly, however, $$DelayedB$$ serves as a powerful instrument for $$Redundant$$, with an F-statistic in the first stage for $$Redundant$$ of 166, significant at the 1% level. Similarly, the associated F-statistic for $$CompSpread \times DelayedB$$ in the first stage for $$CompSpread \times Redundant$$ is 484, significant at the 1% level. 19 Of course, it is also not clear why lenders should have less information than the econometrician in this setting. Actual comparable report dates could be generated in real time by any banker who valued them simply by recording additions to the LPC database feed in real time. 20 Baa–Aaa spreads and the VIX are taken from the St. Louis Federal Reserve Bank data repository and are monthly averages. The D/P ratio of the S&P 500 was taken from Bob Shiller’s website. 21 We have chosen to use the 2SLS framework because it provides information on the full path of influence of the aggregate information, but we might have alternatively just reported reduced-form regressions of loan spreads on the instruments. Such an exercise would mechanically generate coefficients exactly equal to the product of our first- and second-stage coefficients. 22 This result does not appear to hinge importantly on any specific time period. In unreported results, the effect is minimally changed if we focus on the financial crisis (2008–09) or if we exclude the crisis from our sample. References Addoum, J. , and Murfin J. . 2017 . Hidden in plain sight: Equity price discovery with informed private debt. Working Paper . Banerjee, A. V. 1992 . A simple model of herd behavior. Quarterly Journal of Economics 107 : 797 – 817 . Google Scholar CrossRef Search ADS Bikhchandani, S. , Hirshleifer D. , and Welch I. . 1992 . A theory of fads, fashion, custom, and cultural change as informational cascades. Journal of Political Economy 100 : 992 – 1026 . Google Scholar CrossRef Search ADS Bordalo, P. , Gennaioli N. , and Shleifer A. . 2018 . Diagnostic expectations and credit cycles. Journal of Finance 73 : 199 – 227 . Google Scholar CrossRef Search ADS Chodorow-Reich, G. 2014 . The employment effects of credit market disruptions: Firm-level evidence from the 2008–9 financial crisis. Quarterly Journal of Economics 129 : 1 – 59 . Google Scholar CrossRef Search ADS Da, Z. , and Huang X. . 2016 . Harnessing the wisdom of crowds. Working Paper , University of Notre Dame and Michigan State University . Dell’Ariccia, G. , and Marquez R. . 2006 . Lending booms and lending standards. Journal of Finance 61 : 2511 – 46 . Google Scholar CrossRef Search ADS DeMarzo, P. M. , Vayanos D. , and Zwiebel J. . 2003 . Persuasion bias, social influence, and unidimensional opinions. Quarterly Journal of Economics 118 : 909 – 68 . Google Scholar CrossRef Search ADS Dougal, C. , Engelberg J. , Parsons C. A. , and Van Wesep E. D. . 2015 . Anchoring on credit spreads. Journal of Finance 70 : 1039 – 80 . Google Scholar CrossRef Search ADS Eyster, E. , and Rabin M. . 2010 . Naïve herding in rich-information settings. American Economic Journal: Microeconomics 2 : 221 – 43 . Google Scholar CrossRef Search ADS Eyster, E. , and Rabin M. . 2014 . Extensive imitation is irrational and harmful. Quarterly Journal of Economics 129 : 1861 – 98 . Google Scholar CrossRef Search ADS Fama, E. , and French K. . 1997 . Industry costs of equity. Journal of Financial Economics 43 : 153 – 93 . Google Scholar CrossRef Search ADS Glaeser, E. L. , and Nathanson C. G. . 2017 . An extrapolative model of house price dynamics. Journal of Financial Economics 126 : 147 – 70 . Google Scholar CrossRef Search ADS Gorton, G. B. , and He P. . 2008 . Bank credit cycles. Review of Economic Studies 75 : 1181 – 214 . Google Scholar CrossRef Search ADS Graham, J. R. 1999 . Herding among investment newsletters: Theory and evidence. Journal of Finance 54 : 237 – 68 . Google Scholar CrossRef Search ADS Greenwood, R. , and Hanson S. G. . 2013 . Issuer quality and corporate bond returns. Review of Financial Studies 26 : 1483 – 525 . Google Scholar CrossRef Search ADS Griliches, Z. , and Hausman J. A. . 1986 . Errors in variables in panel data. Journal of Econometrics 31 : 93 – 118 . Google Scholar CrossRef Search ADS Ivashina, V. 2009 . Asymmetric information effects on loan spreads. Journal of Financial Economics 92 : 300 – 319 . Google Scholar CrossRef Search ADS Kim, M. , and Ritter J. . 1999 . Valuing IPOs. Journal of Financial Economics 53 : 409 – 37 . Google Scholar CrossRef Search ADS Murfin, J. , and Petersen M. . 2016 . Loans on sale: Credit market seasonality, borrower need, and lender rents. Journal of Financial Economics 121 : 300 – 326 . Google Scholar CrossRef Search ADS Purnanandam, A. K. , and Swaminathan B. . 2004 . Are IPOs really underpriced? Review of Financial Studies 17 : 811 – 48 . Google Scholar CrossRef Search ADS Rajan, R. G. 1994 . Why bank credit policies fluctuate: A theory and some evidence. Quarterly Journal of Economics 399 – 441 . Rhodes, T. 2008 . Syndicated lending-practice and documentation . 5th ed . London : Euromoney . Ruckes, M. 2004 . Bank competition and credit standards. Review of Financial Studies 17 : 1073 – 102 . Google Scholar CrossRef Search ADS Staiger, D. , and Stock J. . 1997 . Instrumental variables regression with weak instruments. Econometrica 65 : 557 – 86 . Google Scholar CrossRef Search ADS Stock, J. , and Yogo M. . 2005 . Testing for weak instruments in linear iv regression , 80 – 108 . New York : Cambridge University Press . Taylor, A. , and Sansone A. . 2006 . The handbook of loan syndications and trading . New York : McGraw-Hill Education . Welch, I. 1992 . Sequential Sales, Learning, and Cascades. Journal of Finance 47 : 695 – 732 . Google Scholar CrossRef Search ADS Welch, I. 2000 . Herding among security analysts. Journal of Financial Economics 58 : 369 – 96 . Google Scholar CrossRef Search ADS Wooldridge, J. M. 2010 . Econometric analysis of cross section and panel data . Cambridge, MA : MIT Press . © The Author(s) 2018. Published by Oxford University Press on behalf of The Society for Financial Studies. All rights reserved. For permissions, please e-mail: journals.permissions@oup.com. This article is published and distributed under the terms of the Oxford University Press, Standard Journals Publication Model (https://academic.oup.com/journals/pages/about_us/legal/notices) http://www.deepdyve.com/assets/images/DeepDyve-Logo-lg.png The Review of Financial Studies Oxford University Press

# Comparables Pricing

, Volume Advance Article – Apr 23, 2018
50 pages

/lp/ou_press/comparables-pricing-0W9FZVmZid
Publisher
Oxford University Press
Abstract Finance professionals commonly set prices based on the analysis of recently closed, comparable transactions. Using data on syndicated loans, we exploit the lag between loans’ closing dates and their inclusion in a widely used comparables database to identify the effect of past transactions on new transaction pricing. Comparables pricing is an important determinant of individual loan spreads, but a failure to account for overlap in information across loans leads to pricing mistakes. Comparables used repeatedly are overweighted as they develop redundant channels of influence on later transactions. Market conditions prevailing at the time a comparable was priced also unduly influence subsequent loans. Received May 23, 2016; editorial decision January 23, 2018 by Editor Robin Greenwood. Comparables pricing, a valuation method in which agents pricing new transactions explicitly weight the prices of similar, recently closed deals, is arguably the dominant approach to pricing in initial public offerings, mergers and acquisitions, loan and bond markets, real estate, venture capital, and private equity. Given its prominence across a range of markets and the sheer size of those markets, this simple approach to valuation plays a large role in how prices are formed in the economy, yet there is little previous research to help us understand its implications. In this paper, we quantify the effect of comparables analysis on equilibrium prices and show that it can result in prices that are biased in predictable ways. At first glance, it may appear easy to motivate comparables pricing as a form of optimal observational learning—agents pricing new transactions incorporate the private information of others in the economy through the examination of past transactions. Yet, we argue that the correct use of comparables is, in fact, nontrivial and that a basic rule-of-thumb implementation can lead to pricing errors. In particular, suppose that agents aggregate all available information—public and private—when setting prices in any given period. Then all transactions priced during that period would reflect the same shared set of public information, though different pieces of private information. Any attempt to aggregate the private information in recently closed transactions (say, by taking some sort of average of their prices) risks overweighting the public information that is shared across comparables. Properly accounting for this interdependence requires complicated and counterintuitive adjustments to the otherwise-straightforward pricing method.1 At the same time, failing to make these adjustments leads to prices that are wrong conditional on the available information. In this paper, we use the market for corporate loans as a laboratory to explore how agents use comparables to form prices and the implications for equilibrium pricing dynamics. We show that comparables are an important determinant of individual loan spreads in practice, but that a failure to correct for the overlapping information across loans leads to pricing mistakes. The loan market provides an ideal setting in which to study the role of comparables in price formation for a variety of reasons. Unlike the stock market, for example, where prices are set more continually, the rate-setting process for a new loan provides an obvious, salient moment at which the price is set, allowing us to more cleanly identify the effect of comparables on subsequent prices. It is also a market where we observe a large volume of new issuance transactions in any given year. Finally, in this market we can accurately identify when information on pricing terms of past transactions became available to other market participants, which allows us to overcome an immediate identification challenge. Specifically, the interest rate spread of a new loan may be correlated with those of recently closed transactions through two channels: either because the new loan explicitly weighted the past transactions, or because they were jointly influenced by the same economic fundamentals. The first contribution of the paper is to separately identify these two channels using information on when loan terms were made available to nonparticipant banks and were thus eligible to be used broadly for pricing new loans. We use the timing of publication of loan terms to a widely used comparables database as a shock to the information set of lead arranger banks. This allows us to estimate the influence a loan spread has on subsequent transactions as its covariation with spreads on similar loans after being publicly revealed (capturing a causal effect plus the effect of common fundamentals) minus the covariation with similar deals occurring before the comparable was known to the market (the effect of common fundamentals).2 By focusing on within-comparable variation in influence before versus after reporting, we also net out potentially confounding effects of loans that went unreported due to unobservable characteristics that might make them less relevant to subsequent transactions. We find that the interest rate spread on an individual comparable has an average influence of 6–10% on the rate set on subsequent loans. Given these magnitudes, we show that any hypothetical pricing errors would have significant spillovers on related transactions in a world with repeated and recursive use of comparables. Armed with the ability to identify the influence a comparable has on new transactions, we turn our attention to a series of tests that discriminate between optimal use of comparables and a form of naïve inference that treats individual comparables as independent signals. To motivate these tests, consider the following instructive example of a hypothetical series of syndicated loans in a particular industry together with their comparables, consisting of similarly rated borrowers in the same industry. For each of the three loans, we report a truncated list of comparables that a lead arranger might have used when pricing the transaction. Figure 1 reflects the standard practice of using a handful of recent transactions as comparables for each new transaction. Figure 1 View largeDownload slide Recursive use of comparables The figure shows a hypothetical sequence of related transactions and their corresponding comparables. Figure 1 View largeDownload slide Recursive use of comparables The figure shows a hypothetical sequence of related transactions and their corresponding comparables. Note that, upon closing, each transaction joins its own comparables in the set of potential comparables for the next transaction. This highlights an immediate potential source of overlapping information. Specifically, the private information used to price Alpha Inc. influences the price of Bravo Group. Then, when agents price Charlie Corp., the prices of both Bravo Group and Alpha Inc. reflect that same private information. By the time Delta Ltd. is priced, all three comparables shown in the figure share the information originally used to price Alpha Inc. Absent complicated adjustments to account for the redundancy of that information, the Alpha Inc. transaction will effectively be triple counted by the agents pricing Delta Ltd., as a result of its previous influence on both Bravo Group and Charlie Corp. Whereas we have no reason to believe the relevance of Alpha Inc. to each subsequent transaction should be increasing (indeed, it is more likely to be decreasing due to the passage of time), a simple prediction based on naïve inference is that its influence will, in fact, grow with repeated use as a comparable. We test this prediction for our sample of loans and matched comparables and find that the influence of a comparable evolves as it is matched to more and more new transactions, as we would expect if lenders fail to account for information overlap. Whereas a comparable is given a weight of roughly 7% by the first transaction for which it might be informative, its influence grows to 13–15% by the time it has matched to five or more transactions. This pattern is difficult to reconcile with a fully rational model of learning. While the influence of a comparable on a new transaction should be independent of how many intervening transactions there happen to be, the results described earlier suggest that bankers may not be properly accounting for the multiple channels of influence that arise from the recursive use of comparables. To isolate this mechanism directly, we again exploit variation in loan reporting dates. This time, however, rather than simply counting the times a comparable might have been used, we identify actual paths of influence on subsequent loans and then use reporting dates along those paths as a shock to the potential magnitude of information overlap. We begin by searching our data for loan triplets like Alpha, Bravo, and Charlie in the earlier example, where, with prompt reporting, the first transaction would have served as a comparable for the second, and both transactions would have served as comparables for the third. Thus, as in the case of Alpha, Bravo, and Charlie, Alpha stands to influence Charlie both directly and indirectly by way of the intervening loan to Bravo. We then measure the actual number of paths of influence a loan like Alpha could have on Charlie based on (i) whether or not it was reported in time to influence Bravo, and (ii) whether or not Bravo was reported in time to pass that redundant influence on to Charlie. Although it is difficult to conceive of an environment where the appropriate influence of the first loan on the third depends on its use as a comparable for intervening transactions or the reporting of those transactions, we find this is indeed the case. Using the earlier example, Alpha’s influence on Charlie is three to five percentage points higher when Alpha is reported in time to influence Bravo, and Bravo is reported in time to influence Charlie. This constitutes a substantial portion of the baseline level of influence for the average comparable of 6–10% presented earlier. Consequently, equilibrium prices are determined not only by the relevant information available in the market, but also, in large part, by the history of that information’s use. In addition to using comparables, lenders consider the history of macroeconomic conditions when setting interest rates. Yet, to the extent those conditions are persistent, they may already be accounted for in the prices of their comparables. Thus, macroeconomic conditions constitute a second source of redundant information that bankers might potentially overweight when using comparables. Returning to the example from Figure 1, prevailing macroeconomic conditions at the end of 2010 will influence all three comparables for Delta. If that information is subsumed by contemporaneous conditions accounted for directly by Delta’s banker, then through naïve use of comparables, the banker may inadvertently (over)weight stale macroeconomic news. Our final tables show that, in addition to being influenced by contemporaneous macroeconomic conditions, spreads on new loans are influenced by the macroeconomic environment that prevailed at the time their comparables were priced. That is, spreads are lower when comparables were priced in good economic times, holding fixed current conditions. These effects are economically significant. A doubling of the average spread on comparables due to aggregate variation in Baa–Aaa spreads, stock market dividend/price ratios, or aggregate volatility at the time comparables closed translates into a 57% increase in a new loan’s spread relative to loans priced at the same point in time but based on different comparables. As before, this suggests that prices depend not only on the set of information available to agents, but also on how prior agents used that information. Finally, using dealer quotes on a subset of the affected loans that trade in an increasingly liquid secondary market, we find that loans priced at high (low) interest rates based on the influence of stale macroeconomic information via their comparables tend to appreciate (depreciate) in value in the six to twelve months post-issuance, affirming our interpretation of the observed dependence on lagged macroeconomic conditions as an error in at-issue pricing. Our paper builds on a number of important papers across a broad range of research areas. Use of comparables as a pricing methodology has received some attention, notably within the literature on initial public offerings (IPOs). Kim and Ritter (1999) and Purnanandam and Swaminathan (2004) both examine IPO pricing and performance through the lens of comparables analysis. Our paper is also related to the literature on information aggregation in settings characterized by social learning, beginning with the theoretical work on rational herding by Bikhchandani, Hirshleifer, and Welch (1992) and Banerjee (1992), with complementary empirical work on herding among investment newsletters and security analysts (Graham 1999; Welch 2000). More recently, Da and Huang (2016) show that herding results in inferior earnings forecasts. Our focus on the consequences of agents incorrectly treating past transactions as independent signals is most closely related to what DeMarzo, Vayanos, and Zwiebel (2003) and Eyster and Rabin (2010, 2014) term “persuasion bias” or “naïve herding,” respectively. Glaeser and Nathanson (2017) develop and test a model of house prices in which agents make similar inferential mistakes. Finally, the paper relates to the literature on credit cycles and rate setting behavior of banks (Rajan 1994; Ruckes 2004; Dell’Ariccia and Marquez 2006; Gorton and He 2008). Even done properly, comparables pricing has interesting implications for credit dynamics—backwards-looking pricing implies slow credit recoveries after recessions and aggressive lending into deteriorating fundamentals. We also contribute to a growing body of theory and evidence that variation in credit pricing may result from biases in the formation of expectations by lenders (Greenwood and Hanson 2013; Bordalo, Gennaioli, and Shleifer 2018; Dougal et al. 2015). 1. Hypothesis Development In this section, we describe a stylized economic environment to motivate and analyze the use of comparables pricing. The purpose is to develop intuition about the proper use of comparables and to motivate testable predictions that will help us distinguish between optimal and naïve use of comparables in the data. To fix ideas, define comparables pricing as a method of valuing an asset by weighting recent transactions on similar assets (the comparables) and private information about the asset value. We begin by describing the conditions under which comparables pricing is optimal. We then show that in a more realistic information environment, comparables pricing results in suboptimal prices. In particular, agents overweight any information that is redundant across comparables at the expense of nonredundant information. Consider a setting in which prices of assets ($$p$$) are driven by a latent economic factor $$F$$ that we will refer to as “fundamentals.” Fundamentals are persistent and have dynamics given by $$F_t = \rho F_{t-1} + v_t, \label{fundamentals}$$ (1) where $$v$$ is Gaussian white noise with variance $${\sigma}^2_v.$$ In each period an agent needs to estimate fundamentals in order to value an asset. The agent’s objective is to get the value of the asset right, and he is penalized for pricing errors in either direction. For convenience, assume that the penalty for getting prices wrong is symmetric and quadratic so that the agent sets prices based on an unbiased, minimum mean-squared-error estimate of $$F$$; that is, $$p_t=\hat{F_t}$$. In setting prices, agents have access to the full history of prices set by others. Each agent collects information about the asset and about the state of the economy, resulting in a signal of fundamentals given by $$s_t = F_t + u_t, \label{signal}$$ (2) where $$u$$ is Gaussian white noise with variance $${\sigma}^2_u$$ and is independent of $$v$$. Given the signal, the full history of prices, and the understanding that yesterday’s prices were set rationally, the best estimate of fundamentals is given by a simple application of the Kalman filter. Prices are formed recursively by updating the last period’s price to account for new information: $$p_t = w_t \times \rho p_{t-1} + (1-w_t) \times s_t, \label{recprices}$$ (3) where $$w_t$$ is a precision weight and converges to a constant in the steady state.3 Two points are worth emphasizing. First, since optimal prices are a precision-weighted average of past prices and current information, comparables pricing (done correctly) is optimal. Of course, the agent needs to assign the correct weights to past transactions and to his own signal, but in this simple setting these weights are readily accessible. Second, as (3) makes clear, only the most recent transaction should receive any explicit weight. This is because $$p_{t-1}$$ fully reflects all of the information available through time $$t-1$$. Instead of using a single comparable as prescribed by Equation (3), in practice, agents typically use several past transactions, perhaps motivated by the notion that separate transactions contain independent information. While this notion is incorrect in the simple environment with one transaction each period, in more general settings it is not difficult to justify.4 In general, the information embedded in the price of any potential comparable can be partitioned into a component that is unique to that comparable and a component that overlaps with the information available in other comparables. Using multiple comparables may serve to aggregate the independent pieces of information but also introduces the risk of double-counting information that is redundant across those transactions. If agents fail to account for the complex aggregation of information represented by their comparables, in what (testable) ways do we expect their mistakes to manifest? To answer this question, consider a special case of Equation (1) with $$\rho=1$$ and $${\sigma}^2_v=0$$, so that each agent simply estimates an unobservable constant F using a private signal and past transactions. There are three periods and four transactions, with two transactions occurring at time 2. Our interest is in the pricing of the final transaction, D. Panel A of Figure 2 shows the signal received by each agent. At time 1 the only available information in the economy is the first signal, so the agent uses that to price transaction A. The agent pricing transaction B equally weights his own signal of 1.4 and transaction A’s price of 0.6 to arrive at a price of 1.0. The agent pricing transaction C follows the same process to arrive at a price of 0.9. Figure 2 View largeDownload slide Comparables pricing example Each panel in the figure shows a sequence of transactions with their corresponding signals and prices. Signals are noisy estimates of the latent fundamentals that agents are trying to match with their prices. Time starts at $$t=1$$, so transaction A’s price equals its signal. Later transactions are able to observe prior transactions (except where noted in panel C). Our interest is the pricing of transaction D, for which the pricing equation is written out on the bottom of each panel. Signals are the same across all panels, but prices depend on whether agents use comparables optimally and whether each past transaction is observable. Figure 2 View largeDownload slide Comparables pricing example Each panel in the figure shows a sequence of transactions with their corresponding signals and prices. Signals are noisy estimates of the latent fundamentals that agents are trying to match with their prices. Time starts at $$t=1$$, so transaction A’s price equals its signal. Later transactions are able to observe prior transactions (except where noted in panel C). Our interest is the pricing of transaction D, for which the pricing equation is written out on the bottom of each panel. Signals are the same across all panels, but prices depend on whether agents use comparables optimally and whether each past transaction is observable. At the time transaction D is priced, there are four total signals available in the economy, each of which should receive an optimal weight of 0.25 (since each is equally informative to D, given our assumption that $$\rho=1$$ and $${\sigma}^2_v=0$$). Of course, since each comparable presents independently useful information, the observability of any one comparable will also hold sway over the final transaction pricing. For example, because A has the lowest price of the three comparables, removing it from the available information set will raise prices in subsequent transactions. Our first and most basic tests in the paper confirm this prediction, with a focus on specific magnitudes of influence. Prediction 1: Prices vary based on which past transactions were reported and when they were reported. But now note that, assuming all transactions were reported, to correctly price D using comparables, a sophisticated agent would need to negatively weight transaction A (as shown in the pricing equation for transaction D), since prices of B and C already account for signal A. The need to negatively weight transactions when using multiple comparables is quite general; this is a central point in Eyster and Rabin (2014). Any time that multiple comparables were influenced by a common piece of information, the source of that common information must be anti-imitated. This can be very complicated when the common source of information was a shared comparable, since the shared comparable will generally comprise a complex aggregation of information, only some of which needs to be anti-imitated. Anti-imitating shared comparables, then, can lead to over-anti-imitating some information, necessitating still further corrections. In short, getting pricing right with multiple comparables is both difficult and counterintuitive. In contrast to the optimal use of comparables, panel B illustrates naïve pricing of transaction D by an agent who views past transactions as if they were simply signals. In this case, the agent weights each past transaction and his own signal equally.5 Obviously, the price of D is wrong, given the incorrect weighting of information. Naïve use of comparables leads to the information in A being overweighted at the expense of information in B and C. Moreover, this naïve use of comparables results in prices that are not uniquely determined by the set of information in the economy. Instead, prices depend on who used which transactions as comparables in the past. To see this, consider panel C, where we examine the pricing that obtains from naïve inference in a modified case where the relevant signals are unchanged, but we assume that it is common knowledge that B did not use transaction A in its pricing. Comparing panels B and C, the final influence of signal A on D (and the resulting price for D) depends on how many intervening agents chose A as a comparable. This gives us our first two related predictions regarding naïve inference, which we test in Tables 3 and 4: Prediction 2a: Comparables will become more influential with each repeated use. Prediction 2b: Comparables that were used to price more intervening co-comparables will be more influential. Table 3 Repeated comparable use Combined Unreported comps Reported comps Loan spread (1) (2) (3) (4) (5) Comp Spread 0.632*** 0.579*** 0.675*** (0.033) (0.055) (0.024) Comp Spread $$\times$$ 2nd Match (Unreported) –0.023 –0.024 (0.029) (0.023) Comp Spread $$\times$$$$\geq$$ 3rd Match (Unreported) –0.037 –0.008 (0.045) (0.028) Comp Spread $$\times$$ 1st Match (Reported)a 0.066** 0.068*** (0.030) (0.026) Comp Spread $$\times$$ 2nd Match (Reported) 0.075** 0.071** (0.035) (0.031) Comp Spread $$\times$$ 3rd Match (Reported) 0.130*** 0.104*** (0.037) (0.035) Comp Spread $$\times$$ 4th Match (Reported) 0.133*** 0.117*** (0.042) (0.040) Comp Spread $$\times$$$$\geq$$ 5th Match (Reported)b 0.149*** 0.128*** (0.047) (0.043) (b)–(a) 0.083*** 0.060** Comp Spread $$\times$$ Number Prior Matches –0.020 0.022*** 0.020** (0.027) (0.008) (0.009) Number Prior Matches 0.079 –0.103** –0.106** (0.139) (0.041) (0.047) Other Controls YES YES YES YES YES Comp Fixed Effects NO YES NO NO YES Number of Comparables 2,990 2,990 2,990 2,990 2,990 Number of Observations 17,319 17,319 5,433 11,886 11,886 $$R^2$$ 0.502 0.770 0.472 0.515 0.805 Combined Unreported comps Reported comps Loan spread (1) (2) (3) (4) (5) Comp Spread 0.632*** 0.579*** 0.675*** (0.033) (0.055) (0.024) Comp Spread $$\times$$ 2nd Match (Unreported) –0.023 –0.024 (0.029) (0.023) Comp Spread $$\times$$$$\geq$$ 3rd Match (Unreported) –0.037 –0.008 (0.045) (0.028) Comp Spread $$\times$$ 1st Match (Reported)a 0.066** 0.068*** (0.030) (0.026) Comp Spread $$\times$$ 2nd Match (Reported) 0.075** 0.071** (0.035) (0.031) Comp Spread $$\times$$ 3rd Match (Reported) 0.130*** 0.104*** (0.037) (0.035) Comp Spread $$\times$$ 4th Match (Reported) 0.133*** 0.117*** (0.042) (0.040) Comp Spread $$\times$$$$\geq$$ 5th Match (Reported)b 0.149*** 0.128*** (0.047) (0.043) (b)–(a) 0.083*** 0.060** Comp Spread $$\times$$ Number Prior Matches –0.020 0.022*** 0.020** (0.027) (0.008) (0.009) Number Prior Matches 0.079 –0.103** –0.106** (0.139) (0.041) (0.047) Other Controls YES YES YES YES YES Comp Fixed Effects NO YES NO NO YES Number of Comparables 2,990 2,990 2,990 2,990 2,990 Number of Observations 17,319 17,319 5,433 11,886 11,886 $$R^2$$ 0.502 0.770 0.472 0.515 0.805 The table measures the growth in influence of a comparable as it is matched to an increasing number of new transactions. Columns 1 and 2 interact $$CompSpread$$ with dummies for the number of loans a comparable has matched to before and after being reported. The excluded category is the first pre-reported match. Column 2 adds comparable fixed effects. Columns 3 through 5 estimate the growth in influence parametrically by interacting the comparable’s number of prior matches with $$CompSpread$$. Column 3 does this only for comparables before they are reported, while Columns 4 and 5 focus on the same comparables after they are reported, with and without comparable fixed effects. All regressions include controls for comparable age and precision as well as their interactions with $$CompSpread$$, as described in Table 2. Standard errors are reported in parentheses and are clustered at the level of comparable firm and borrowing firm. ***, **, and * indicate significance at the 1%, 5%, and 10% levels, respectively. Table 3 Repeated comparable use Combined Unreported comps Reported comps Loan spread (1) (2) (3) (4) (5) Comp Spread 0.632*** 0.579*** 0.675*** (0.033) (0.055) (0.024) Comp Spread $$\times$$ 2nd Match (Unreported) –0.023 –0.024 (0.029) (0.023) Comp Spread $$\times$$$$\geq$$ 3rd Match (Unreported) –0.037 –0.008 (0.045) (0.028) Comp Spread $$\times$$ 1st Match (Reported)a 0.066** 0.068*** (0.030) (0.026) Comp Spread $$\times$$ 2nd Match (Reported) 0.075** 0.071** (0.035) (0.031) Comp Spread $$\times$$ 3rd Match (Reported) 0.130*** 0.104*** (0.037) (0.035) Comp Spread $$\times$$ 4th Match (Reported) 0.133*** 0.117*** (0.042) (0.040) Comp Spread $$\times$$$$\geq$$ 5th Match (Reported)b 0.149*** 0.128*** (0.047) (0.043) (b)–(a) 0.083*** 0.060** Comp Spread $$\times$$ Number Prior Matches –0.020 0.022*** 0.020** (0.027) (0.008) (0.009) Number Prior Matches 0.079 –0.103** –0.106** (0.139) (0.041) (0.047) Other Controls YES YES YES YES YES Comp Fixed Effects NO YES NO NO YES Number of Comparables 2,990 2,990 2,990 2,990 2,990 Number of Observations 17,319 17,319 5,433 11,886 11,886 $$R^2$$ 0.502 0.770 0.472 0.515 0.805 Combined Unreported comps Reported comps Loan spread (1) (2) (3) (4) (5) Comp Spread 0.632*** 0.579*** 0.675*** (0.033) (0.055) (0.024) Comp Spread $$\times$$ 2nd Match (Unreported) –0.023 –0.024 (0.029) (0.023) Comp Spread $$\times$$$$\geq$$ 3rd Match (Unreported) –0.037 –0.008 (0.045) (0.028) Comp Spread $$\times$$ 1st Match (Reported)a 0.066** 0.068*** (0.030) (0.026) Comp Spread $$\times$$ 2nd Match (Reported) 0.075** 0.071** (0.035) (0.031) Comp Spread $$\times$$ 3rd Match (Reported) 0.130*** 0.104*** (0.037) (0.035) Comp Spread $$\times$$ 4th Match (Reported) 0.133*** 0.117*** (0.042) (0.040) Comp Spread $$\times$$$$\geq$$ 5th Match (Reported)b 0.149*** 0.128*** (0.047) (0.043) (b)–(a) 0.083*** 0.060** Comp Spread $$\times$$ Number Prior Matches –0.020 0.022*** 0.020** (0.027) (0.008) (0.009) Number Prior Matches 0.079 –0.103** –0.106** (0.139) (0.041) (0.047) Other Controls YES YES YES YES YES Comp Fixed Effects NO YES NO NO YES Number of Comparables 2,990 2,990 2,990 2,990 2,990 Number of Observations 17,319 17,319 5,433 11,886 11,886 $$R^2$$ 0.502 0.770 0.472 0.515 0.805 The table measures the growth in influence of a comparable as it is matched to an increasing number of new transactions. Columns 1 and 2 interact $$CompSpread$$ with dummies for the number of loans a comparable has matched to before and after being reported. The excluded category is the first pre-reported match. Column 2 adds comparable fixed effects. Columns 3 through 5 estimate the growth in influence parametrically by interacting the comparable’s number of prior matches with $$CompSpread$$. Column 3 does this only for comparables before they are reported, while Columns 4 and 5 focus on the same comparables after they are reported, with and without comparable fixed effects. All regressions include controls for comparable age and precision as well as their interactions with $$CompSpread$$, as described in Table 2. Standard errors are reported in parentheses and are clustered at the level of comparable firm and borrowing firm. ***, **, and * indicate significance at the 1%, 5%, and 10% levels, respectively. Of course, to get pricing right, agents would need to keep track of (or estimate) the reporting dates of past transactions in order to know what was observable and when, which may be a high hurdle. If we think it would be too difficult for market participants to keep track of which information is redundant, then maybe we should not be surprised to find them neglecting redundancy. Our final tests, however, isolate a set of information embedded in comparables that almost certainly is common knowledge and, hence, should not be subject to risk of overweighting by good Bayesian lenders. Specifically, to the extent an agent pricing a new transaction is influenced by the current state of the macroeconomy, he ought to understand that the same was also true for the agents pricing his comparables in prior periods. And since information on relevant macroeconomic conditions contemporaneous with the closing of his comparables is readily available, a sophisticated agent should be able to filter out the now-extraneous influence of older macroeconomic news on his comparables. In contrast, if agents use comparables naïvely, stale macroeconomic information will be transmitted to new transactions through their comparables. In Tables 5 and 6, we test this prediction: Prediction 3: New transactions are influenced by the macroeconomic conditions that prevailed at the time their comparables were priced, leading to under- or overpricing at issuance. Table 5 Aggregate dynamics under comparables pricing Panel A—First Stage Average Comp Spread (1) (2) (3) (4) $$\overline{\text{Baa-Aaa Spread}}$$ (at comp closing) 0.248*** 0.113** (0.042) (0.047) $$\overline{\text{Market D/P}}$$ (at comp closing) 36.174*** 13.170* (5.468) (6.878) $$\overline{\text{VIX}}$$ (at comp closing) 1.167*** 0.734*** (0.146) (0.181) $$R^2$$ 0.862 0.862 0.868 0.868 F-statistic (excluded instruments) 35.01 43.47 63.23 21.96 p-value of F-statistic 0.00 0.00 0.00 0.00 Panel B—Second Stage Loan spread (1) (2) (3) (4) Average Comp Spread 0.337* 0.623*** 0.645*** 0.567*** (0.173) (0.167) (0.137) (0.138) Year $$\times$$ Month Fixed Effects YES YES YES YES Rating and Industry Fixed Effects YES YES YES YES Loan Controls YES YES YES YES Number of Months 324 324 300 300 Number of Observations 25,820 25,820 25,374 25,374 Panel A—First Stage Average Comp Spread (1) (2) (3) (4) $$\overline{\text{Baa-Aaa Spread}}$$ (at comp closing) 0.248*** 0.113** (0.042) (0.047) $$\overline{\text{Market D/P}}$$ (at comp closing) 36.174*** 13.170* (5.468) (6.878) $$\overline{\text{VIX}}$$ (at comp closing) 1.167*** 0.734*** (0.146) (0.181) $$R^2$$ 0.862 0.862 0.868 0.868 F-statistic (excluded instruments) 35.01 43.47 63.23 21.96 p-value of F-statistic 0.00 0.00 0.00 0.00 Panel B—Second Stage Loan spread (1) (2) (3) (4) Average Comp Spread 0.337* 0.623*** 0.645*** 0.567*** (0.173) (0.167) (0.137) (0.138) Year $$\times$$ Month Fixed Effects YES YES YES YES Rating and Industry Fixed Effects YES YES YES YES Loan Controls YES YES YES YES Number of Months 324 324 300 300 Number of Observations 25,820 25,820 25,374 25,374 The table reports the first and second stages of a 2SLS model of logged loan spreads on the average of logged comparable spreads using variation from prevailing market conditions at the time of the comparables as an instrument. The unit of observation is the loan being priced. Comparables are matched as described in Section 2.2. Both stages include controls for borrower rating and industry (Fama French 30 industries), the logged loan size, and logged maturity in months. Additionally, the first stage presented in panel A includes the Baa–Aaa spread, the aggregate dividend/price level of the S&P 500, and/or the level of the VIX that prevailed at the time the comparables were priced, averaged over a loan’s comparables, as excluded instruments. Panel A reports the impact of these aggregate pricing signals on the average comparable. Panel B then reports the second stage of the 2SLS model to show how that effect is passed on to the loan being priced. All regressions include monthly time fixed effects as of the loan closing date. Standard errors are reported in parentheses and are clustered at the level of the borrowing firm and month. ***, **, and * indicate significance at the 1%, 5%, and 10% levels, respectively. Table 5 Aggregate dynamics under comparables pricing Panel A—First Stage Average Comp Spread (1) (2) (3) (4) $$\overline{\text{Baa-Aaa Spread}}$$ (at comp closing) 0.248*** 0.113** (0.042) (0.047) $$\overline{\text{Market D/P}}$$ (at comp closing) 36.174*** 13.170* (5.468) (6.878) $$\overline{\text{VIX}}$$ (at comp closing) 1.167*** 0.734*** (0.146) (0.181) $$R^2$$ 0.862 0.862 0.868 0.868 F-statistic (excluded instruments) 35.01 43.47 63.23 21.96 p-value of F-statistic 0.00 0.00 0.00 0.00 Panel B—Second Stage Loan spread (1) (2) (3) (4) Average Comp Spread 0.337* 0.623*** 0.645*** 0.567*** (0.173) (0.167) (0.137) (0.138) Year $$\times$$ Month Fixed Effects YES YES YES YES Rating and Industry Fixed Effects YES YES YES YES Loan Controls YES YES YES YES Number of Months 324 324 300 300 Number of Observations 25,820 25,820 25,374 25,374 Panel A—First Stage Average Comp Spread (1) (2) (3) (4) $$\overline{\text{Baa-Aaa Spread}}$$ (at comp closing) 0.248*** 0.113** (0.042) (0.047) $$\overline{\text{Market D/P}}$$ (at comp closing) 36.174*** 13.170* (5.468) (6.878) $$\overline{\text{VIX}}$$ (at comp closing) 1.167*** 0.734*** (0.146) (0.181) $$R^2$$ 0.862 0.862 0.868 0.868 F-statistic (excluded instruments) 35.01 43.47 63.23 21.96 p-value of F-statistic 0.00 0.00 0.00 0.00 Panel B—Second Stage Loan spread (1) (2) (3) (4) Average Comp Spread 0.337* 0.623*** 0.645*** 0.567*** (0.173) (0.167) (0.137) (0.138) Year $$\times$$ Month Fixed Effects YES YES YES YES Rating and Industry Fixed Effects YES YES YES YES Loan Controls YES YES YES YES Number of Months 324 324 300 300 Number of Observations 25,820 25,820 25,374 25,374 The table reports the first and second stages of a 2SLS model of logged loan spreads on the average of logged comparable spreads using variation from prevailing market conditions at the time of the comparables as an instrument. The unit of observation is the loan being priced. Comparables are matched as described in Section 2.2. Both stages include controls for borrower rating and industry (Fama French 30 industries), the logged loan size, and logged maturity in months. Additionally, the first stage presented in panel A includes the Baa–Aaa spread, the aggregate dividend/price level of the S&P 500, and/or the level of the VIX that prevailed at the time the comparables were priced, averaged over a loan’s comparables, as excluded instruments. Panel A reports the impact of these aggregate pricing signals on the average comparable. Panel B then reports the second stage of the 2SLS model to show how that effect is passed on to the loan being priced. All regressions include monthly time fixed effects as of the loan closing date. Standard errors are reported in parentheses and are clustered at the level of the borrowing firm and month. ***, **, and * indicate significance at the 1%, 5%, and 10% levels, respectively. Table 6 Aggregate dynamics and loan mispricing Panel A: First stage Average Comp Spread (1) $$\overline{\text{Baa-Aaa Spread}}$$ (at comp closing) 0.041 (0.069) $$\overline{\text{Market D/P}}$$ (at comp closing) 29.400*** (10.550) $$\overline{\text{VIX}}$$ (at comp closing) 0.874*** (0.313) Observations 3,330 $$R^2$$ 0.753 F-statistic (excluded instruments) 28.49 p-value of F-statistic 0.00 Panel A: First stage Average Comp Spread (1) $$\overline{\text{Baa-Aaa Spread}}$$ (at comp closing) 0.041 (0.069) $$\overline{\text{Market D/P}}$$ (at comp closing) 29.400*** (10.550) $$\overline{\text{VIX}}$$ (at comp closing) 0.874*** (0.313) Observations 3,330 $$R^2$$ 0.753 F-statistic (excluded instruments) 28.49 p-value of F-statistic 0.00 Panel B: Second stage 3-month 6-month 9-month 12-month Loan Post-Issuance Price Change (1) (2) (3) (4) Average Comp Spread 0.012 0.044** 0.057** 0.062* (0.014) (0.021) (0.025) (0.037) Year $$\times$$ Month Fixed Effects YES YES YES YES Rating and Industry Fixed Effects YES YES YES YES Loan Controls YES YES YES YES Number of Observations 2,909 2,978 2,932 2,824 Panel B: Second stage 3-month 6-month 9-month 12-month Loan Post-Issuance Price Change (1) (2) (3) (4) Average Comp Spread 0.012 0.044** 0.057** 0.062* (0.014) (0.021) (0.025) (0.037) Year $$\times$$ Month Fixed Effects YES YES YES YES Rating and Industry Fixed Effects YES YES YES YES Loan Controls YES YES YES YES Number of Observations 2,909 2,978 2,932 2,824 The table reports the first and second stage of a 2SLS model of loan post-issuance price changes on the average of logged comparable spreads using variation from prevailing market conditions at the time of the comparables as an instrument. Price changes are calculated from the month after loan closing to 3, 6, 9, or 12 months thereafter. Data on loan values come from mark-to-market quotes aggregated across dealers by the Loan Syndications and Trading Association. Observations are at the loan level, and comparables are matched as described in Section 2.2. Both stages include controls for borrower rating and industry (Fama French 30 industries), the logged loan size, and logged maturity in months. Additionally, the first stage presented in panel A includes the Baa–Aaa spread, the aggregate dividend/price level of the S&P 500, and/or the level of the VIX that prevailed at the time the comparables were priced, averaged over a loan’s comparables, as excluded instruments. Panel A reports the impact of these aggregate pricing signals on the average comparable. Panel B then reports how that effect is passed on to the subsequent price changes of the affected loans. All regressions include monthly time fixed effects as of the loan closing date. Standard errors are reported in parentheses and are clustered at the level of the borrowing firm and month. ***, **, and * indicate significance at the 1%, 5%, and 10% levels. Table 6 Aggregate dynamics and loan mispricing Panel A: First stage Average Comp Spread (1) $$\overline{\text{Baa-Aaa Spread}}$$ (at comp closing) 0.041 (0.069) $$\overline{\text{Market D/P}}$$ (at comp closing) 29.400*** (10.550) $$\overline{\text{VIX}}$$ (at comp closing) 0.874*** (0.313) Observations 3,330 $$R^2$$ 0.753 F-statistic (excluded instruments) 28.49 p-value of F-statistic 0.00 Panel A: First stage Average Comp Spread (1) $$\overline{\text{Baa-Aaa Spread}}$$ (at comp closing) 0.041 (0.069) $$\overline{\text{Market D/P}}$$ (at comp closing) 29.400*** (10.550) $$\overline{\text{VIX}}$$ (at comp closing) 0.874*** (0.313) Observations 3,330 $$R^2$$ 0.753 F-statistic (excluded instruments) 28.49 p-value of F-statistic 0.00 Panel B: Second stage 3-month 6-month 9-month 12-month Loan Post-Issuance Price Change (1) (2) (3) (4) Average Comp Spread 0.012 0.044** 0.057** 0.062* (0.014) (0.021) (0.025) (0.037) Year $$\times$$ Month Fixed Effects YES YES YES YES Rating and Industry Fixed Effects YES YES YES YES Loan Controls YES YES YES YES Number of Observations 2,909 2,978 2,932 2,824 Panel B: Second stage 3-month 6-month 9-month 12-month Loan Post-Issuance Price Change (1) (2) (3) (4) Average Comp Spread 0.012 0.044** 0.057** 0.062* (0.014) (0.021) (0.025) (0.037) Year $$\times$$ Month Fixed Effects YES YES YES YES Rating and Industry Fixed Effects YES YES YES YES Loan Controls YES YES YES YES Number of Observations 2,909 2,978 2,932 2,824 The table reports the first and second stage of a 2SLS model of loan post-issuance price changes on the average of logged comparable spreads using variation from prevailing market conditions at the time of the comparables as an instrument. Price changes are calculated from the month after loan closing to 3, 6, 9, or 12 months thereafter. Data on loan values come from mark-to-market quotes aggregated across dealers by the Loan Syndications and Trading Association. Observations are at the loan level, and comparables are matched as described in Section 2.2. Both stages include controls for borrower rating and industry (Fama French 30 industries), the logged loan size, and logged maturity in months. Additionally, the first stage presented in panel A includes the Baa–Aaa spread, the aggregate dividend/price level of the S&P 500, and/or the level of the VIX that prevailed at the time the comparables were priced, averaged over a loan’s comparables, as excluded instruments. Panel A reports the impact of these aggregate pricing signals on the average comparable. Panel B then reports how that effect is passed on to the subsequent price changes of the affected loans. All regressions include monthly time fixed effects as of the loan closing date. Standard errors are reported in parentheses and are clustered at the level of the borrowing firm and month. ***, **, and * indicate significance at the 1%, 5%, and 10% levels. 2. Data and Sample Construction Our empirical work depends on the ability to estimate the causal impact that a comparable’s price has on a new transaction. Yet the economic environment described above suggests that this causal impact will be difficult to identify because of the comparable’s correlation with the agent’s private signal or other unobservable (to the econometrician) information used to price the new transaction. Put plainly, two similar, successive transactions will tend to have similar prices because they are exposed to the same economic fundamentals, even in the absence of direct influence. If we were, then, to naïvely regress prices of new transactions on prices of publicly known comparable transactions, the estimated coefficient would contain both the causal impact of the comparable’s price on the new transaction and any correlation caused by common exposure to fundamentals.6 To separate the two effects, we might look for random variation in past prices that is uncorrelated with fundamentals, but this seems hard to imagine. Instead, we approach the identification problem by looking for an appropriate control group against which to benchmark the effect of comparables on subsequent prices—a placebo group for which there could have been no causal effect, but which would allow us to net out the bias described above. In theory, we could search for two sets of comparables for each transaction being priced. The first set would consist of publicly known transactions that could have been plausibly used by an agent pricing new transactions. The second set would consist of otherwise similar transactions, but which, for some exogenous reason, could not have been used as comparables because they were not observable to the pricing agent. Even better, we might examine the covariation of a single set of comparables with subsequent transactions both immediately prior to and immediately after they are publicly reported. In this idealized setting, subtracting the covariation of current prices with comparables not yet known to the market (the effect of common fundamentals) from the covariation of current transaction prices with comparables prices after the comparables were publicly revealed (the causal effect plus the effect of common fundamentals) would isolate the causal effect of past prices on the prices of new transactions. We do our best to replicate the setting described in the previous paragraph by turning to the corporate loan market. In addition to being a large and important source of capital for firms as well as a significant source of revenue for banks—in 2014, Thomson Reuters reported that new U.S. loan originations totaled $${\}$$2.3 trillion and generated bank fees in excess of $${\}$$12.1 billion (Thomson Reuters 2014 Global Syndicated Loans Review)—the loan market also serves as a natural laboratory to explore comparables use, given that, anecdotally, lenders often justify loan terms based on the analysis of recently closed transactions.7 Meanwhile, since the lead arranger on a new issue loan sets interest rates as of a fixed date, we can more cleanly identify the influence of comparables than we could in, say, the stock market, where prices are set on a more continual basis.8 Moreover, we will also argue that within this market, we know something about when lenders would have become aware of past transactions, giving us the opportunity to vary the observability of a comparable and thus tease out its causal influence. Specifically, we focus on the reporting practices of a widely used loan database and associated trade publication that has been the prevailing source used by lenders to research comparable transactions since the late 1980s. The database, known to practitioners as Loan Pricing Corporation’s Loan Connector (LPC or LPC’s Loan Connector), is familiar to academics when sold in a raw database format as DealScan. In its web-based format, Loan Connector is used as the dominant tool for researching recent market activity, featuring a searchable database of closed loans and their key terms. The population of the database, although partially based on parsing Securities and Exchange Commission (SEC) disclosures made by public borrowers, is also largely driven by lenders who report loans to LPC in order to receive credit in the company’s sister publication Gold Sheets’ quarterly league tables. League tables rank lead arranger banks based on the number and volume of transactions closed. The incentive to be highly ranked in league tables is strong, given that this is often a central component of a bank’s standard pitch book to borrowers. Thus, lenders report their loans, although perhaps not immediately, to the database in order to maximize their placement in league table rankings. Competing products exist globally (notably, LoanWare, linked to Euromoney, is relevant in Europe), but in the United States conversations with active lenders suggest that Loan Connector is by far the dominant source of information for reviewing recent market activity. If LPC is a sufficiently important source of information to lead arrangers pricing new loans, then we can exploit inference about when transactions are included in the database as a source of variation in the set of comparables available to a lender.9 In the extreme, if the banker’s information set were completely determined by LPC’s reporting (and we could observe the timing of LPC’s reporting with 100% accuracy), we would converge on the idealized experiment described, whereby unreported comparables serve as a perfect control group. Of course, in practice, we recognize that LPC reporting dates give us an imperfect control group. Lenders have other information about loan market activity. They will be aware of transactions in which they participated or considered participating. They may have conversations with rival lenders about market activity. Finally, our estimates of LPC reporting dates are themselves noisy. While our identification doesn’t require a one-to-one matching between reporting dates and the information set of a lead arranger, a weak relationship between the two would likely cause us to have low-powered tests and the attendant problems thereof. The idealized experiment described also presumes that delays in LPC’s reporting are as good as random, an assumption that is likely to fail in practice. As we go forward, we will, therefore, wish to be careful to consider the extent to which our proposed methodology is working as we would expect.10 With this in mind, we proceed with a discussion on how we recover the reporting date for loans followed by the details on data construction and regression specifications. 2.1 Recovering reporting dates The key input into our analysis is the date on which loans are reported to the LPC database. To identify this, we lean on the fact that PackageIDs—unique identifiers assigned to each loan package in DealScan—are assigned in the order that loans are recorded in the database. This gives us a perfect rank ordering of when transactions were reported, regardless of when they actually closed. In Figure 3, we show a scatter plot of the PackageIDs and the DealActiveDates (typically the closing date or the effective date of the loan, when legal documents become effective). From this we can see clearly that transactions are not always reported at the time of closing. As an example, note the hanging mass of points with PackageIDs close to 10,000 in the first panel of Figure 3. Given the proximity of their PackageIDs, we know that these deals were reported close to the same time, despite the fact that their actual closing dates range from 1981 to 1992. When were these transactions actually reported? Obviously the answer is not 1981, since there were transactions reported at the same time that did not close until 1992. Instead, if for that group of PackageIDs, at least a few were reported on time, then a sensible estimate of the reporting date would be the latest closing date within the group. In this particular case, that would be January 1992. More generally, this date can be estimated as the upper boundary of the scatter plot. The second panel in Figure 3 illustrates the effect of backfill on this scatter plot by zooming in on the transactions occurring during 2007–08. Each observation is labeled with the date the data were downloaded based on two download vintages (2008 and 2014). Notice clearly that observations on the interior of the scatter plot are reported late and thus only appear in the later vintage of the data, despite the fact that most closed in time for inclusion in the 2008 cut. Figure 3 View largeDownload slide PackageIDs and closing dates The figure shows a scatter plot of PackageIDs and DealActiveDates for the DealScan database. The first panel shows the entire scatter plot with a line estimating the 99th percentile upper boundary. The second panel zooms in on closing dates in 2007–08. In the second panel, dots are labeled with the download vintage (2008 or 2014) of the data. Dots on the interior of the scatter plot were reported late, as none show up in the 2008 vintage of the database. Figure 3 View largeDownload slide PackageIDs and closing dates The figure shows a scatter plot of PackageIDs and DealActiveDates for the DealScan database. The first panel shows the entire scatter plot with a line estimating the 99th percentile upper boundary. The second panel zooms in on closing dates in 2007–08. In the second panel, dots are labeled with the download vintage (2008 or 2014) of the data. Dots on the interior of the scatter plot were reported late, as none show up in the 2008 vintage of the database. Thus, we proceed by estimating the upper boundary of the scatter plot of loan dates and deal identifiers by running a quantile regression of the closing date for the loan on the PackageID and the squared PackageID. The quadratic term allows for the curvature of the boundary. We use a rolling quantile regression estimated at the 99th percentile, where each regression includes 15,000 PackageIDs and the regressions are rolled forward with a step-size of 5,000 observations. Average fitted values from the rolling regressions identify the upper boundary of the plot, shown as the solid blue line in the first panel of Figure 3. Finally, because the 99th percentile is arbitrary, we calibrate the fitted dates such that the median transaction was reported within two weeks of closing in the last full year for which we have data.11 This is based on claims by the data provider that the “majority of transactions” are reported within two weeks. The resulting mapping for each PackageID reflects our estimate of the deal reporting date for every transaction in the data.12 For the full sample, this results in an average reporting delay—the time between closing and the loan being reported—of 66 days, but a standard deviation of just over six months. Over the entire sample period, we estimate that 58% of facilities were reported within one month of their deal closing date, although the timeliness of reporting improves over time. Since 2010, for example, 79% of facilities were reported within of a month of the closing date, whereas in 1990 only 9% of facilities were reported within a month. To confirm the reasonableness of our estimates and to highlight the incentives that drive reporting of loans to a data provider like LPC, Figure 4 shows the mean reporting delay for loans originated in different months of the year. Given that incentives to report loans are determined by the desire to be included in league tables prepared by Thomson Reuters/Gold Sheets using LPC’s database (league tables that are reported widely in the financial press), we expect to see that lenders will report transactions more quickly when prompt reporting is necessary to receive credit for transactions in the year-end and quarter-end league tables. Figure 4 confirms this. Whereas median reporting time is less than three weeks in the final month of each quarter, the median reporting delay extends to 35 days in January, immediately following the year-end league table deadline, as bankers have less incentive to promptly report recently closed transactions. While we do not directly exploit this source of variation in reporting date (Murfin and Petersen (2016) show there exist notable borrower selection effects associated with loan closing dates), it is reassuring that our estimates of reporting dates are consistent with what one would expect given the incentives to report. Figure 4 View largeDownload slide Reporting delay by closing month The figure shows the median delay between the closing date of a loan and our estimated loan reporting date as a function of the month of closing. A quarterly pattern is evident, as loans are reported more quickly the closer they are to quarter end. Figure 4 View largeDownload slide Reporting delay by closing month The figure shows the median delay between the closing date of a loan and our estimated loan reporting date as a function of the month of closing. A quarterly pattern is evident, as loans are reported more quickly the closer they are to quarter end. 2.2 Comparable matching With estimates of the date on which LPC published the terms of various loans to its database, we now can track the influence of these loans on future transactions by other lenders. The next challenge, however, is to identify likely candidate comparables for each new transaction. This is nontrivial. However, in the event that we fail in some or even many cases, this will tend to bias our estimates of a comparable’s influence downwards. To identify sensible comparables, we use a matching algorithm that sorts through transactions closed at least 30 days prior to the closing date of the loan of interest but not more than one year prior to that. The slight lag accommodates the gap between the time a loan is priced and its closing date. Within that subset of loans, we look within industry, using Fama and French’s 30-industry classification (Fama and French 1997), and within loan type, where loan type is a data field that distinguishes term loans from revolvers, commercial paper backup facilities, 364-day facilities, banker’s acceptance lines, and so on. Following the suggestions of practitioners active in the market, we also require that short-term loans match to short-term loans and long-term loans match to long-term loans, where long-term (short-term) is defined as maturities longer than or equal to (shorter than) 60 months. Within these groups, finally, we match based on closeness of Standard and Poor’s long-term debt rating of the issuer, Moody’s corresponding issuer rating, or the average of the two for dual-rated issuers, where averages are constructed based on a numerical rating assignment ranging from 2 (AAA) to 24 (C). Ratings are as of the date of loan closing and are reported by LPC. Of course, this forces us to limit the sample to loans for which the borrower had a long-term issuer rating at the time of closing, but it also gives us freedom to include private firms in the sample for which we do not have accounting information (leverage, for example) on which we might otherwise match firms. By forcing the match to occur along one dimension, we are also able to accommodate fuzzy matches without resorting to weighting matrices to scale distance over multiple dimensions. We ensure that matched transactions are separated by no more than one major ratings category (e.g., a BB+ rated loan can match to loans rated from B+ to BBB+) by requiring that the difference in numerical ratings between matches does not exceed three. We generally think this replicates a natural search procedure an analyst might perform when looking for comparables using LPC’s interface—search by industry and loan characteristics, and then look for similarly rated borrowers within that cohort. Using these criteria, each loan is matched to its nearest acceptable comparables: loans that share an industry, loan type, and maturity class, and have a maximum ratings distance of one major ratings category. Finally, we cap the number of comparables a given loan can have such that the average transaction has five reported matches. In the event of ties, we pick comparables with the closest loan maturity and then closest loan amount. Choosing a specific cap to the number of potential comparables is necessary to avoid transactions with an implausibly large number of matches dominating the sample. Moreover, it is important for our empirical tests that we avoid false positives in our matching algorithm to the extent possible. While the failure to identify actual matches limits our test power by restricting sample size, the erroneous identification of irrelevant matches both reduces power and induces a downward bias in many of our basic tests. Conversations with bankers suggest that a typical transaction would likely consider three to seven comparables. Our baseline results use a cap of seven matches per transaction to deliver an average of five. However, in the Appendix we show that we can cap the number of matches at five or ten (for average match numbers of 3.8 and 6.9, respectively) with limited effect on the paper’s core results. After completing the initial matching exercise, we are left with 26,325 transactions being priced by 25,656 distinct comparables. Each facility has an average of 5.4 comparables (5.0 of which are reported, by design), with a maximum of seven and a minimum of one. The average comparable, meanwhile, is used to price 5.5 loans (5.1 loans after being reported). Finally, to sharpen our categorization of which comparables were visible and which were invisible to a given lead arranger, for our initial tests we also drop any observations where the lead arranger of the new transaction was in the syndicate for its comparable. The loan characteristics of the transactions being priced and their matched comparables are presented in panel A of Table 1. We see that, with the exception of loan size, the two groups are on average very similar, at least in terms of maturity, ratings, and spreads. This is not surprising; after all, today’s new transaction will serve as tomorrow’s comparable. The only material difference—loan size—can be explained by the combination of growth in nominal issuance sizes over time and the fact that comparables must occur before matched transactions. Table 1 Summary statistics Panel A Facilities priced Comparables N Mean Median S.D. N Mean Median S.D. $$\Delta$$ Means Facility Amount ($${\}$$M) 23,934 491.8 250.0 870.9 23,108 462.3 235.0 802.1 –29.5*** Maturity (months) 23,934 50.17 60 24.13 23,108 50.11 60 23.97 –0.06 Numerical Avg LT Debt Rating (2-24) 23,934 13.40 14 3.53 23,108 13.41 14 3.47 0.01 Loan Spread 23,934 204.9 175.0 153.3 23,108 206.0 175.0 152.9 1.11 Panel B Unreported comparables Reported comparables N Mean Median S.D. N Mean Median S.D. $$\Delta$$ Means Facility Amount ($${\}$$M) 3,966 318.3 150.0 588.7 22,132 468.1 250.0 807.5 149.8*** Maturity (months) 3,966 44.74 48 24.02 22,132 50.29 60 23.87 5.55*** Numerical Avg LT Debt Rating (2-24) 3,966 13.37 14 3.39 22,132 13.41 14 3.47 0.04 Loan Spread 3,966 183.6 150.3 136.6 22,132 206.4 175.0 152.9 22.8*** Panel A Facilities priced Comparables N Mean Median S.D. N Mean Median S.D. $$\Delta$$ Means Facility Amount ($${\}$$M) 23,934 491.8 250.0 870.9 23,108 462.3 235.0 802.1 –29.5*** Maturity (months) 23,934 50.17 60 24.13 23,108 50.11 60 23.97 –0.06 Numerical Avg LT Debt Rating (2-24) 23,934 13.40 14 3.53 23,108 13.41 14 3.47 0.01 Loan Spread 23,934 204.9 175.0 153.3 23,108 206.0 175.0 152.9 1.11 Panel B Unreported comparables Reported comparables N Mean Median S.D. N Mean Median S.D. $$\Delta$$ Means Facility Amount ($${\}$$M) 3,966 318.3 150.0 588.7 22,132 468.1 250.0 807.5 149.8*** Maturity (months) 3,966 44.74 48 24.02 22,132 50.29 60 23.87 5.55*** Numerical Avg LT Debt Rating (2-24) 3,966 13.37 14 3.39 22,132 13.41 14 3.47 0.04 Loan Spread 3,966 183.6 150.3 136.6 22,132 206.4 175.0 152.9 22.8*** Panel C Switching comparables N Mean Median S.D. Facility Amount ($${\}$$M) 2,990 313.6 150.0 565.2 Maturity (months) 2,990 44.27 47 23.36 Numerical Avg LT Debt Rating (2-24) 2,990 13.30 14 3.29 Loan Spread 2,990 179.1 150.0 131.1 Panel C Switching comparables N Mean Median S.D. Facility