Haughwout, Hyman, Shachar, The Option Value of Municipal Liquidity: Evidence from Federal Lending Cutoffs during COVID-19 (NY Fed Staff Report 988, 2021-10)
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Federal Reserve Bank of New York Staff Reports, no. 988, dated October 2021, titled The Option Value of Municipal Liquidity: Evidence from Federal Lending Cutoffs during COVID-19, by Andrew Haughwout, Benjamin Hyman, and Or Shachar. The abstract states that the authors use a regression discontinuity design based on lending eligibility population cutoffs of the Municipal Liquidity Facility to study effects on yields, primary debt issuance, and public sector employment. It states that the announcement of the liquidity option improved overall municipal bond market functioning and that lower-rated issuers additionally benefited from direct access to the facility. It also states that local governments responded by recalling a greater share of service-providing government employees.
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The Option Value of Municipal
NO. 988
OCTOBER 2021 Liquidity: Evidence from Federal
Lending Cutoffs during COVID-19
Andrew Haughwout | Benjamin Hyman | Or Shachar
The Option Value of Municipal Liquidity:
Evidence from Federal Lending Cutoffs during COVID-19
Andrew Haughwout, Benjamin Hyman, and Or Shachar
Federal Reserve Bank of New York Staff Reports, no. 988
October 2021
JEL classification: G14, G18, H74
Abstract
We estimate the option value of municipal liquidity by studying bond market activity and
public sector hiring decisions when government budgets are severely distressed. Using a regression
discontinuity (RD) design, we exploit lending eligibility population cutoffs introduced by the federal
sector’s Municipal Liquidity Facility (MLF) to study the effects of an emergency liquidity option on
yields, primary debt issuance, and public sector employment. We find that while the announcement
of the liquidity option improved overall municipal bond market functioning, lower-rated issuers
additionally benefited from direct access to the facility—their bonds traded at higher prices and
were issued more frequently, suggesting a potential credit-risk sharing channel on top of the Fed’s
role as liquidity-provider of last resort. Local governments, by contrast, responded to emergency
liquidity measures by recalling a greater share of service-providing government employees (mostly
educational institution workers), but recalls were only sustained for higher-rated municipalities. This
hiring responsiveness is consistent with the hypothesis that large government furloughs might have
over-weighted the worst possible outcomes based on past experience. Together, the results suggest
that municipalities would likely have been more distressed absent the emergency liquidity.
Key words: municipal debt, state and local governments, COVID-19, Federal Reserve lending facilities
_________________
Haughwout, Hyman, Shachar: Federal Reserve Bank of New York, IZA (email:
andrew.haughwout@ny.frb.org, ben.hyman@ny.frb .org, or.shachar@ny.frb.org). The authors thank
Rebecca Landau, Nicholas Ritter, and Christopher Simard for outstanding research assistance. They
especially thank John Bagely, Nick Frost, Kent Hiteshew, Matt Lieber, and Shawn Nee for their
continued assistance with the data and expert guidance on the institutional details concerning the muni
market. They also thank Kirill Borusyak, Anthony DeFusco, Gilles Duranton, Dan Garrett, Daniel Green,
Paul Goldsmith-Pinkham, Bev Hirtle, Bob Inman, Ben Keys, Anna Kovner, Byron Lutz, Melissa Moye,
and Wilbert van der Klaauw, for valuable feedback on their early-stage results, and various seminar
participants from the Virtual Municipal Finance Workshop, UC Irvine, NYU Furman, the UEA Annual
Meetings, the Federal Reserve System Regional Meetings, the Brookings Municipal Finance Conference,
and the NBER Summer Institute for their comments. Lastly, they thank Gray et al. (2020) for sharing
their codebase.
This paper presents preliminary findings and is being distributed to economists and other interested
readers solely to stimulate discussion and elicit comments. The views expressed in this paper are those of
the author(s) and do not necessarily reflect the position of the Federal Reserve Bank of New York or the
Federal Reserve System. Any errors or omissions are the responsibility of the author(s).
To view the authors’ disclosure statements, visit
https://www.newyorkfed.org/research/staff_reports/sr988.html.
1 Introduction
The State and Local sector is the dominant government service provider in the US, employing nearly 20
million workers. State and local government activity directly contributed 10.9 percent of GDP in 2019,
well above the federal sector’s direct contribution of 6.6 percent (BEA, 2020). A long-standing debate
in public and macroeconomics concerns the optimal level of debt with respect to growth rates, yet less
is known about the extent to which municipalities are liquidity constrained and thus what the value of
lifting such constraints would entail for welfare, especially in periods of fiscal distress.
Particularly important to municipal functioning but often overlooked is the short-term municipal
bond market, which can serve as a clearing house when expenditures and revenue receipts are
temporarily misaligned. This happens, for example, when tax payments arrive on specific dates (e.g.
quarterly), while payroll and other expenses are typically more continuous. In these circumstances,
municipalities access short-term funding markets to allow them to maintain smooth spending paths,
secured with future revenue. These smoother municipal funding paths have at least two potential real
economy benefits: they may curtail pro-cyclical fiscal policies that result in layoffs or furloughs; they
can also support positive externalities emanating from high fiscal multipliers (Chodorow-Reich (2019),
Yi (2020)) or the municipality’s unique role as coordinating agent—especially salient after a natural
disaster or health crisis when effective emergency services (such as hospitals reliant on public revenue)
can reduce the duration of economic downturns (Auerbach et al. (2020)).
In this paper, we estimate the option value of municipal liquidity by studying bond market activity
and public sector hiring decisions when government budgets are severely distressed. Using a regression
discontinuity (RD) design, we exploit lending eligibility cutoffs introduced by the Federal sector’s
Municipal Liquidity Facility (MLF) in April 2020 that granted direct Federal Reserve lending eligibility
(via a Special Purpose Vehicle backstopped by an initial US Treasury equity investment) to city issuers
with populations greater than 250,000, and county issuers with populations greater than 500,000.1
Combining the cross-sectional variation from the RD with the timing of the policy announcement helps
us overcome the empirical challenge of separately identifying the effects of one Federal intervention
(MLF) from the many others that were simultaneously implemented around this period.2 One such
1 These cutoffs announced on April 27, 2020, expanded eligibility beyond the original April 9, 2020 cutoffs of 1m and 2m
for cities and counties respectively, granting access to most but not all issuers (see Section 2 for further details). We call this
the “option value” because despite finding large effects on yields, only two issuers actually made use of the facility from its
inception through December 2020. In this sense, the RD can be thought of as more of an intent-to-treat estimator where the
liquidity option is imperfectly taken up but the MLF option is fully salient.
2 For example, on April 9th, the MLF was announced as part of a broader $2.3 trillion package including support for the
Payroll Protection Program (PPP), Main Street Lending program, expansions to corporate credit facilities (PMCCF and SMCCF)
as well as the Term Asset-Backed Securities Loan Facility (TALF). This underscores the difficulties in using timing alone to
isolate the effects of the MLF, and the importance of using cross-sectional variation for identification.
1
confounder is the CARES Act Coronavirus Relief Fund (CRF) announced one month earlier which
provided direct aid to cities and counties with populations over 500,000, thus sharing one of the two
cutoffs used for MLF lending. The later timing of the MLF allows us to isolate effects separately from
CRF aid, while the cross-sectional variation from the RD further minimizes selection concerns that would
arise from comparing all eligible versus non-eligible issuers (endogenous correlates of city size which
may also predict municipal performance).
We first document that overall secondary market yields and primary issuance for the most part
returned to normal market functioning following the totality of Federal interventions that were
introduced between mid-March and the end of April 2020, while low-rated investment grade bonds
remained relatively distressed. We then estimate the effect of differential MLF access using municipal
bond yields as an investor-perceived valuation of access to emergency liquidity, allowing us to learn
how the market assessed the marginal borrower’s liquidity constraint. We find that low-rated (A and
BBB) city and county issuers’ bonds traded at higher prices immediately following facility access, but
did not respond to direct CARES aid announced over a month earlier using a similar eligibility cutoff.
Low-rated issuers that were narrowly eligible for emergency lending exhibited a yields decline
(demand increase) of roughly 75 basis points relative to observationally equivalent issuers that narrowly
missed eligibility—a sizable magnitude that closely resembles the overall market spread between BBB
yields and higher-rated issuers. These differences in investor perceptions also translated to a large
differential increase in primary issuance among low-rated issuers, but new bonds were not issued
directly through the MLF. That is, while there were too few facility users to test whether the MLF directly
facilitated additional revenue smoothing among issuers, their ability to issue at favorable borrowing
costs on private markets clearly improved with the facility option. These results imply that absent the
MLF, issuers would have likely been constrained in their ability to issue new debt throughout the crisis.
We then turn to real-side employment outcomes, and ask whether emergency liquidity induced local
budget officers to retain more public sector employees or increase hours in light of mass furloughs and
separations. There are at least two mechanisms through which the provision of such liquidity could be
related to employment decisions. First, as noted above, short-term borrowing may serve to preserve
the cash flow required to maintain employment when receipt of revenues is delayed or otherwise
mismatched with the timing of payroll. Second, and less obvious, is a long-term debt refunding channel.
By facilitating the issuance of debt at lower cost, the availability of liquidity may allow the issuer to lower
its debt service costs through refunding, thereby freeing up additional resources for service provision.
This second channel is especially relevant when interest rates are falling, as they were during the early
stages of the COVID-19 pandemic.
2
We find that city and county governments recalled more service-providing government employees
in response to the totality of both the MLF option and direct CARES aid, however, decomposition
tests suggest that hiring mostly responded to CARES aid and not the MLF option (consistent with
recent work by Green and Loualiche (2020)). In our preferred specification, eligible issuers retained
about 422 to 517 more local service-providing employees relative to observationally equivalent local
governments in the two months following the cutoff announcement. On a baseline year-on-year decline
of about 1,717 employees, this reflects a substantial recovery effect size of roughly 25% to 30%. Almost
all of the retained service-providing employees were concentrated in Education and Health Services, the
majority of which is comprised of educational institution employees.3 Consistent with priority hiring
for education sector employees, year-on-year RD estimates are positive during lockdown months, revert
to zero during summer months when school labor demand is low, with recalls sustaining beyond the
summer for high-rated governments (the vast majority of issuers). The result that less fiscally constrained
governments appear more elastic in hiring (especially while shutdowns were largely still in place) is
consistent with the hypothesis that state and local governments may have over-weighted the worst
possible outcomes based on past experience, furloughing education sector employees even though
realized revenue shortfalls were far lower than originally anticipated.4
In the remainder of the paper, we probe why MLF access was perceived as more valuable
lower down on the ratings distribution rather than as neutral across the distribution, and discuss
implications for optimal policy. We use two further strategies to gauge the mechanism behind this
result. We first estimate the probability that one of the three major nationally recognized statistical
rating organizations (NRSROs) downgraded any of the issuer’s bonds, and find modest evidence that
downgrade probabilities differentially increased when the issuer was revealed as ineligible for facility
access. Using a complementary asset price decomposition approach following Boyarchenko et al. (2020)
and Schwert (2017), we also quantify the credit-risk channel over a broader set of issuers, which implies
a non-trivial role for credit risk in determining yields during peak distress. These results combined
suggest the presence of a potential credit-risk sharing channel beyond the Federal Reserve’s role as
a liquidity provider of last resort—a willingness to credit-risk share even if not widely exercised in
practice. Interestingly, though the facility terms target primary issuance of notes with maturities of up to
36 months, we find substantial impacts on long-term secondary market yields. One novel contribution
of the paper is thus identifying a feedback channel between short-term primary issuance and long-term
3 One potential political economy interpretation for this concentration is that while furloughs and separations may have
faced less political resistance in sectors with a clear rationale for lockdowns, a liquidity option may have induced the retention
of some of these employees. Another relates to prioritizing unionized workers.
4 This view was articulated in Sheiner (2021), which we discuss along with the evolving fiscal and jobs outlook of state and
local governments in Appendix A.1.
3
secondary market liquidity in the municipal sector, which to our knowledge, has not been previously
documented. One example of how this could happen is short-term notes could be applied to long-term
general obligation (GO) debt servicing. Short-term optionality could enter the operational budget
affecting long term pass-through if localities have flexible constitutions or statues which permit such
fungibility.5
Given our new estimate of credit-risk sharing, a parameter which enters a broader welfare calculus
regarding the efficiency of macroeconomic stabilization policies, one natural question is when does
municipal credit-risk sharing represent a socially efficient policy improvement? From a financial
frictions viewpoint, several influential papers have suggested that sub-optimal risk sharing could arise if
institutional investors are overly concentrated in locally exempt bonds—a home market bias that distorts
the efficient spread of risk (Poterba (1989), Pirinsky and Wang (2011), Schwert (2017), Babina et al.
(2021)). Other market structure constraints may also result in inefficient muni market pricing (Garrett
(2020)). When such frictions are also heterogeneously correlated with the mean income of underlying
geographies, inequality weights must also be taken into consideration. Future work will need to
contextualize the magnitude of potential externalities and multipliers from government functioning
(including the social value of public services) to help answer this question.
1.1 Relevant Literature
The municipal bond literature studying yields has broadly examined default risk, liquidity risk, and
tax effects. Using MSRB transaction-level data, both Wang et al. (2008) and Schwert (2017) attribute
a large proportion of the observed yield to default risk in municipal bond pricing. Using a sample
from 1998 to 2015 (mostly expansion years), Schwert (2017) finds that credit-default risk accounts for
between 74% and 84% of mean spreads; a strikingly large share.6 Ang et al. (2014), however, use a
different approach and find that liquidity accounts for 75% of the average municipal bond spread.7
We interpret our findings as consistent with the Schwert (2017) results, as our estimates of MLF access
imply a large investor perceived spread, but only among the lowest rated issuers, which we interpret
as reflecting credit downgrade (and potentially, but not necessarily, default) risk. Our employment and
5 In related work, we are exploring whether we can leverage differences in these rules and features of outstanding long
term bonds (such as revenue versus GO), to try to address this apparent short-term to long-term mechanism.
6 The estimated range of the credit-default risk component in Schwert (2017) is based on three approaches: measuring the
default component as a residual after adjusting yields for tax and for liquidity components estimated from transactions data
directly; measuring the default component using credit default swaps; and, using within-bond changes in spreads around
pre-refunding events, when a risky bond becomes risk-free, while controlling for bond-specific unobservables using fixed
effects.
7 Ang et al. (2014) compute synthetic risk-free municipal bond yields using an estimated zero-coupon curve from
pre-refunded municipal bonds, adjusting them to have the same liquidity as regular munis, and compute the credit risk
component by taking the difference between regular municipal bond yields and yields computed using the synthetic discount
rates.
4
credit downgrade results are also fully consistent with Adelino et al. (2017), who find that credit ratings
impact borrowing constraints, and subsequently have real implications for employment and expenditure
outcomes; as well as Cornaggia et al. (2018) who find a significant link between credit ratings, yields,
and borrowing costs. We also view our credit-risk sharing results as related to Gao et al. (2019), who
document that the regulatory default environment meaningfully interacts with borrowing costs and
yields.
In a contemporaneous paper, Bi and Marsh (2020) also analyze the impact of varied fiscal and
monetary policy interventions on municipal bond market performance in the wake of COVID-19. Bi
and Marsh (2020) analyze daily time series effects around different announcements and do not focus
explicitly on the MLF nor its associated cutoffs for identification. Like us, they focus on differential high
credit-risk, and find that long-term, low-rated bonds remained distressed beyond Federal interventions.
By contrast, we find that this was only true when the MLF was not available to those issuers. Bordo
and Duca (2021) further focus on the time series impact of the MLF announcement on yields spreads,
and find that the MLF capped the growth of spreads by 5 to 8 percentage points. Li and Lu (2020)
focus on the effects of shutdown announcements on offering yields (rather than traded prices in
the secondary market), and find that initial offering yields increased in response to shutdowns, and
decreased following facility announcements. Both Bordo and Duca (2021) and Li and Lu (2020) are
consistent with our results on market functioning, however, neither focus on the causal effects of MLF
optionality on issuers. Finally, Fritsch et al. (2021) study entities that issued directly through the MLF,
and similarly find that yields declined after announcements of intent to issue via the facility.
Our paper also builds on methodological contributions from a series of municipal bond market
papers, including Harris and Piwowar (2006), Green et al. (2007b), and Green et al. (2010), who study
secondary market transaction costs; and Green et al. (2007a) and Schultz (2012) who focus on the pricing
and price dispersion of newly issued bonds. We also draw from work by Novy-Marx and Rauh (2012)
quantifying the sovereign default channel. Lastly, related to evaluating Federal Reserve facilities, our
methodological approach most closely links to work by Moore (2017) who analyzed the Term Auction
Facility by comparing marginal winners and losers, and Luck and Zimmermann (2020) who find strong
employment effects from quantitative easing (QE) policies via bank lending channels.
Finally, Auerbach et al. (2020) examine federal and state fiscal conditions in the context of the
pandemic, both generating their own estimates and evaluating other papers. They find generally, that
the pandemic has induced smaller tax losses may have been initially expected, for example, when
imputing expected losses from the Great Recession. In Appendix A.1, we further provide a detailed
summary of the evolution of state and local revenue and employment forecasts throughout the pandemic
5
and during the sample frame of this analysis. One specific paper examining the effect of CARES Act aid
on employment during COVID-19, Green and Loualiche (2020), finds that sales-tax reliant localities with
stricter balanced budget requirements (BBRs) (proxied by lower rainy day funds) likely suffered greater
job losses due to an inability to deficit spend across budget cycles, and it was in those cases that fiscal
aid was more effective. This finding, in part, prompts us to include state fixed effects in our preferred
specification to absorb variation across states emanating from the stringency of their underlying BBRs
(however our main results do not rely on these fixed effects).
The rest of the paper proceeds as follows. Section 2 provides institutional background on municipal
debt markets and the unique market distress exhibited during the COVID-19 pandemic. In Section
3, we discuss the main bond market and real economy data sources used, matching procedures and
sample restrictions. Section 4 outlines our methodological approach and estimating equations. Section
5 presents the main results on bond-level outcomes, public sector employment, and mechanism tests.
We provide sensitivity and robustness tests to our results in Section 6, and conclude with a discussion of
what is learned from the main results in light of a perceived low take-up puzzle regarding the number
of issuers that made use of the Municipal Liquidity Facility in Section 7.
2 Municipal Distress and Federal Interventions during COVID-19
Our empirical strategy leverages a unique policy implemented in response to the COVID-19 pandemic.
In this section we discuss municipal bond market conditions in the run-up to the pandemic, how recent
dynamics may have diverged from prior trends and contributed to peak disruption, and a detailed
timeline of Federal sector interventions that supported municipal debt markets during this period.
2.1 Turmoil in Municipal Debt Markets
The Municipal Bond Market
The $3.8 trillion municipal bond market contains more than 50,000 issuers and 1 million individual
bonds, making it approximately half the size of the corporate bond market with 10 times as many issuers.
Roughly 90% of this market is exempt from federal income tax,8 and more than 80% is rated investment
grade. Consequently, municipal bond default rates have historically been low (Appleson et al., 2012).
As of May 2020, 26% of outstanding debt was issued directly by state, city, county, and other local
governments, 41% by utilities, service, and transit issuers, 21% by school districts, and 8% by public
8 Some bonds are “double-exempt” for local residents, applicable to tax liabilities at both Federal and State levels (e.g. CA
state bonds for CA residents), whereas others are “triple-exempt” at the local level as well (e.g. New York City bonds).
6
hospitals. Unlike treasury and corporate bond markets, 70% of municipal debt is held by retail investors
(a third of which is in mutual funds and ETFs) seeking tax advantages associated with municipal bond
returns.9 Unlike the corporate sector, municipal debt is also commonly issued in deals containing many
different tenors as independent bonds, facilitating more predictable budget smoothing.
Government issuers in this market are often required to balance their operating budgets, and can
usually only borrow long term in order to finance infrastructure investments. In 2015, 48 of 50 US
states had some form of balanced budget requirement (BBR), while 39 of 50 had strong constitutional
or statutory requirements (Brookings Tax Policy Center, 2015), limiting deficit spending across fiscal
cycles.10 General Obligation (GO) bonds, which constitute approximately 30% of the long-term
municipal market, are not secured by a specific revenue source but are instead backed by the “full faith
and credit of the taxing authority” and typically finance capital projects like bridges and schools. The
large remainder of the long term market (60%) is dominated by Revenue bonds (RB) issued by public
enterprises and secured by defined revenue sources (such as transit revenue, airport feels, bridge tolls,
etc.)11
Less well known but central to this paper, state and local governments also frequently leverage the
$440 billion short-term municipal note market to bridge cash flow gaps within fiscal years. As localities
depend on revenues (tax receipts, federal grants, the proceeds of bond issues and other revenues) that
are only received at specific intervals, budget officers seek to smooth spending in anticipation of such
receipts, and can do so by issuing TANs, RANs, BANs – tax anticipation notes, revenue anticipation
notes, and bond anticipation notes. Other notes include tax and revenue anticipation notes (TRANs),
tender option bonds (TOBs), and Variable Rate Demand Notes (VRDNs), the latter of which comprises
roughly half of the short term market. Short-term notes are typically secured by the revenues expected
to be received later in the fiscal year, and are paid off when said revenues arrive. A classic example is the
proceeds from final settlements of state income tax returns due April 15 (the federal tax filing deadline),
which can include taxable unearned income and capital gains (typically not withheld). Other examples
include quarterly property tax receipts, or expected surges in airport fees during the holiday season.
Primary market interest rates at which governments issue new debt in this market are also strongly
linked to secondary market yields. This is because primary market pricing is usually benchmarked
to secondary market prices of similar bonds, and the willingness of dealers to underwrite bonds is
impacted by market conditions (Boyarchenko et al., 2020). Price discovery occurs through submissions
9 Outstanding debt by sector calculated from Bloomberg, as of 5/19/2020. Retail share calculated from the Board of
Governors, “Financial Accounts of the United States, Z.1, as of 1Q2020.” Retail holdings calculated from MSRB.
10 Some states further prohibit or limit GO bond issues, including Arizona, Colorado, Idaho, Indiana, Iowa, Kansas,
Kentucky, Nebraska, North Dakota, South Dakota, and Wyoming.
11 MSRB, Bloomberg, calculated as of 5/21/2020.
7
to exchanges, and is exceptionally low in this market in part due to the low volume of transacted trades
(Green et al., 2010). In an average expansion year (such as 2019), muni bonds trade about 6,500 times a
day with median trades of about $30,000, far less frequently and at lower volumes than corporate bonds.
Municipal Liquidity Crisis
While many of these features of the municipal market have remained relatively constant for several
decades, one notable change in recent years has been the increasing share of muni holdings in mutual
funds, which nearly doubled to $800 billion since 2010 (from 10% to 20% of the market) and by some
measures now reflect one third of overall muni holdings (WSJ, Oct 2019). Importantly, municipal
holdings by mutual funds have also become more concentrated, with over 70% of muni mutual funds
held by the 10 largest fund families (investment banks).12
After a record surge of muni inflows into mutual funds that netted $90 billion over the 12 months
ending in February 2020, inflows reversed sharply in March 2020, with municipal bond mutual funds
experiencing outflows of $43 billion in March (Cipriani et al., 2020a). In a rush for liquidity, this
offloading was accompanied by sell-offs in other fixed income asset classes, not just municipal bonds.
As explained in Cipriani et al. (2020a), “When funds experience outflows, fund managers must sell
securities in order to have enough liquidity to meet redemptions. As a result, there was almost no
demand for new issuance at the peak of the market disruption”. Indeed, early on in the pandemic,
some muni market journalists credited increased mutual fund concentration as one potential reason
why municipal markets may have had an unexpectedly outsized role in the rush for liquidity during the
COVID pandemic relative to prior downturns—the ensuing sell-off may have flooded the market due to
seller concentration, bringing muni demand and new debt issuance to a near standstill by mid-March.13
Figure 1 below shows the performance of secondary market municipal bond yields during this
period, and highlights the liquidity crisis that occurred in early- to mid-March.
12 Calculations from “Financial Accounts of the United States, Z.1, as of 1Q2020”.
13 According to the Wall Street Journal, one prominent fund attempted to offload up to $700 million in munis in a single day,
which they note, was an unprecedented contrast to the usual $50,000 trades the market is accustomed to (WSJ, April 2020).
8
Figure 1: Turmoil in Secondary Market Municipal Bond Yields during COVID-19
NOTES—Both panels use daily current yields (6-month) in the calculation of the dependent variable. The left panel
is taken from the AAA BVAL curve from Bloomberg, while both plots’ bonds ratings are calculated as averages
across Moody’s and S&P ratings (take directly from Bloomberg). The three announcements indicated by vertical
dotted lines are described in detail in the text. Source: Bloomberg, originally calculated in Cipriani et al. (2020a).
The left panel shows mean weekly yields for the universe of secondary-market traded AAA muni
bonds—the safest in the market—as a ratio to comparable US treasuries. In the period leading up
to the mid-March turmoil, municipal bonds were trading at yields below US treasuries (ratios below
1) due to their special tax-exempt status. The market then deteriorated in a steep yield rise until the
first Federal intervention in the muni market was announced on March 23 (indicated by the left-most
dotted line, and explained in detail in the subsequent subsection).14 Yields spiked precipitously for
all bond tenors but most sharply for short-run debt, reflecting deteriorating demand conditions as
investors anticipated severe dislocation in the near term.15 After a series of further Federal interventions,
markets finally reverted back to relative market functioning by June. The right pane, however, reveals
significant heterogeneity in this resumption to normalcy—the lowest rated investment-grade bonds
(BBB) continued to exhibit distress despite recovery in lower risk credit bins. One potential explanation
for these heterogeneous recovery rates is that investors may have struggled to assess the change in
credit default risk for low-rated issuers weathering the first wave of the pandemic, consistent with
notoriously low price discovery in municipal markets due to their low trading frequency.16 As Green
et al. (2010) note, illiquid assets may “rise faster than they fall”. This differential recovery motivates
14 This, as well as subsequent interventions relevant to the analysis and marked by the two additional dotted lines in Figure
1, are all described in further detail in the next subsection.
15 It is common practice in the municipal bond market that newly issued bonds target an at-issuance coupon rate of 5% by
modifying initial offering prices. Because coupon interest is fixed at issuance and comprises the numerator of the current yield
metric shown in Figure 2 (with prices reflected in the denominator), large spikes in yields thus tend to reflect declining prices
as demand shifts downward.
16 One additional example of opaqueness in municipal debt markets relates to undisclosed private muni loans, extensively
documented in Ivanov et al. (2021).
9
our main heterogeneous specifications in which we examine effects separately according to pre-crisis
creditworthiness levels, discussed in Section 4.
While secondary market yields provide an important lens for measuring financial distress, the ability
of state and local governments to issue new municipal bonds on primary markets is also critically
linked to secondary market performance. If demand is low for bonds already traded in the market,
then the additional supply of new bonds (like those needed to bridge government cash flow shortfalls)
may be both constrained, and potentially issued at higher cost than during an expansion—even in the
presence of a monetary policy environment with lower prevailing interest rates. Local governments
supplying new bonds in this environment may face increased intermediation fees from market makers
and underwriters seeking to arrange initial offerings, and may have to resort to compensating investors
with high interest rates for retaining illiquid positions or additional credit risk. Figure 2 below shows
2020 weekly new issuance as compared to the minimum and maximum issuance in the same weeks over
the previous five years.
Figure 2: State and Local Government New Issuance Shortfalls during COVID-19
NOTES—Figure shows weekly total primary issuance in the municipal bond market throughout the 2020 calendar
year, compared to the five-year historical maximum and minimum issuance in the same week. Weekly means
are aligned beginning-of-week on Mondays (when most Federal interventions are announced), and may include
refinanced bonds which appear as new CUSIPs. Source: Bloomberg, originally calculated in Cipriani et al. (2020a).
As the pandemic set in, governments endured a clear primary issuance shortfall relative to historical
trend, which approached a market freezing point at its nadir around March 20th. After a series of
Federal interventions, the trend then mean reverts and appears to compensate for missing issuance.
Especially apparent is a significant issuance spike in mid-July, when local and state income tax receipts
and non-withheld income such as capital gains were realized (deferred in 2020 due to the IRS federal tax
10
deadline extension from April 15 to July 15, enacted as a matter of fiscal policy). Cumulatively, though at
least the end of June, 2020 year-to-date primary issuance had narrowly outpaced its five-year historical
levels, though as we discuss below, this uptick may not necessarily reflect the socially efficient level of
primary issuance given the unusual supply needs of municipal issuers during the pandemic.
2.2 Pass-Through of Market Distress to Budgets and the Real Economy
To understand how municipal market liquidity crises impact state and local budgets and public sector
hiring, consider two fiscal cycles spanning one calendar year, as shown in panel (a) of Figure 3.
Figure 3: Fiscal Cycles and Budget Needs during a Municipal Liquidity Crisis
(a) During an expansion year
FY20 Revenue Receipts
FY19 Revenue Receipts
Jan 1 Apr 15 Dec 31
ST Muni Notes (e.g. TANs)
(b) During a liquidity crisis
FY21 Revenue Receipts ↓
FY20 Revenue Receipts ↓
Jan 1 COVID Apr 15 July 15 Dec 31
ST Muni Notes (e.g. TANs) ↑
In a regular calendar year (like 2019), state and local governments incur expenses such as payroll,
debt service, etc., throughout this entire period, but only receive expected revenue at distinct intervals.
One prominent example of an irregular revenue source is the proceeds from final settlements of
state income tax returns, typically due April 15 (the federal tax filing deadline), which can include
taxable unearned income (typically not withheld).17 When governments are short of revenue yet have
guaranteed sources of future receipts, they can issue short-term anticipation notes on municipal bond
markets to help smooth out the temporary shortfall. Take for example, the state of New York, whose
tax base includes large amounts of capital gains realized in the prior calendar year. Taxes on these
amounts are typically received on April 15. New York may issue a 4-month tax anticipation note (TAN)
in anticipation of this revenue on Jan 1, 2019, maturing April 30th, 2019 (one month after its fiscal cycle
17 Other examples include quarterly property tax receipts, or expected surges in airport fees during the holiday season.
11
closes). This would generate bond proceeds to smooth out cash flow, and would be secured by revenue
incoming on April 15, enabling the government to start spending part of the expected settlement amount
in the interim.
Now consider what happens when an economy experiences a major income shock accompanied by
a bond market liquidity crisis, as was the case with the COVID-19 pandemic and the muni market.
There are three distinct ways in which this enters fiscal budgeting, shown in red in panel (b) of Figure
3. First, income receipts decline in both the current and upcoming fiscal cycles. While tax assessments
may be revised downwards, 2021 budgets were for the most part already set when the COVID pandemic
took hold. This led to a decline in the revenue that would normally cover these planned expenditures.
Second, as a matter of fiscal policy, the IRS extended the 2020 federal tax deadline from April to July
15th, increasing the quantity of short-term notes governments desired to issue on the market to plug
the additional cash flow gap. Third, while the temporary misalignment of expenditures and revenue
needs (even if unexpectedly large in a specific year) are normally able to be remedied through the bond
market, the simultaneous large financial sell off of fixed income assets described in Section 2 effectively
drove investor demand for munis toward zero, leaving governments unable to borrow. This was the
challenge faced by the US economy in mid-March of 2020; local governments could not borrow on
private municipal markets despite their increasing need to do so because of demand conditions.
2.3 Federal Interventions during COVID-19
We had to undertake very quickly to enter into the market, and our four principles that were guiding us
in terms of our design were: speed to announcement and execution—do not let the perfect be the enemy
of the good; ensure that State and local governments had access to liquidity for operating cash—this
is what we heard overwhelmingly from individual issuers and associations like GFOA; restore market
confidence and stability given the unprecedented liquidity crisis in the market; and finally, to your
point, to design a uniformly applicable, transparent, easy-to-administer facility.
—Kent Hiteshew, Deputy Associate Director for Financial Stability, Federal Reserve Board of Governors (on
the choice of lending eligibility population cutoffs for the Municipal Liquidity Facility Congressional Oversight
Commission, Examination of the Municipal Liquidity facility Established by the Federal Reserve Pursuant to the
CARES Act, Sept 17, 2020.)
In light of both real municipality liquidity challenges and a municipal market liquidity crisis, several
Federal Sector agencies undertook interventions to influence municipal bond markets. Here, we describe
the three most prominent interventions that relate to this paper, indicated with vertical dotted lines in
12
plots throughout the draft.
March 23, 2020: MMLF Accepts Some Types of Municipal Debt as Collateral: The Federal Reserve System
expanded its recently announced Money Market Mutual Fund Liquidity Facility (MMLF)—which makes
loans to financial institutions secured by high-quality collateral—to accept variable rate muni demand
notes (VRDNs) as pledgable collateral.18 As shown in Figure 1 and Figure 2, the announcement day
of this expansion corresponds almost exactly with the peak of municipal yields and other measures of
market distress, which subsequently began a steady decline to normal market functioning as Federal
demand for municipal assets pulled the market away from its sales freeze. Moving forward, we refer to
the time period prior to this first announcement as the “pre-period” or placebo period when studying
effects of subsequent facility announcements before any were yet established. However, it bears noting
that two days earlier, the Internal Revenue Service (IRS) and US Treasury formally extended the Federal
tax filing deadline from April 15 to July 15 to provide household tax payment relief on 2019 liability
payments due in April.19 Further, on this same day, several new Federal Reserve facilities (for example in
the corporate bond market) were announced or expanded.20 For these reasons, any time series analysis
across these various announcements must be treated delicately as they have the potential to confound
effects from a bundle of interventions. We thus interpret effects of the “totality of events” when analyzing
dependent variables before the first (and after the last) of these announcements are made.
April 9, 2020: Municipal Liquidity Facility (MLF) Announced. As part of a broader $2.3 trillion support
package that included support for the Payroll Protection Program (PPP), Main Street Lending program,
expansions to corporate credit facilities (PMCCF and SMCCF) as well as the Term Asset-Backed
Securities Loan Facility (TALF), the Municipal Liquidity Facility (MLF) was announced on April 9 “to
help state and local governments better manage the cash flow pressures they are facing as a result of the
increase in state and local government expenditures related to the COVID-19 pandemic and the delay
and decrease of certain tax and other revenue.”21 The MLF was established with a $35b US Treasury
initial equity investment (appropriated through the March 27 CARES act) as backstop for a maximum of
$500b in direct Federal Reserve lending of short-term notes (TANs, RANs, TRANs, BANs) to municipal
issuers via a Special Purpose Vehicle (SPV). As the quote above demonstrates, there was considerable
concern in the design phase of the facility that facing up to 50,000 issuers would render the operational
arm of the facility less effective, and risk a slower speed to intervention. Consequently, eligible issuers
18 The MMLF was established “to prevent outflows from prime and muni money market funds from turning into an
industry-wide run, as happened in September 2008”, and was supported by $10 billion of credit protection from the U.S.
Treasury’s Exchange Stabilization Fund. (Cipriani et al., 2020b). While the MMLF had accepted some forms of short-term
municipal debt on March 20, the types of pledgble collateral were greatly expanded on March 23.
19 See March 21, 2020 IRS Extension Announcement for details.
20 See Federal Reserve System Board of Governors Press Release, March 23, 2020 “Federal Reserve announces extensive new
measures to support the economy” for a description.
21 See Federal Reserve Bank of New York MLF Page, April 9, 2020 and April 9, 2020, MLF Term Sheet for further details.
13
were initially limited to US states, cities with populations greater than 1 million, and counties with
population greater than 2 million.
By targeting the largest issuers first (where the bulk of trading occurs), the thinking was that this
push would help the market stabilize, and additional issuers could be covered by the parent state’s
ability to “downstream” to ineligible issuers, as described below.22 Tenors were originally limited to
2-year maturities, and priced at a penalty rate to a private market index by issuer credit rating.23 The
lending eligibility cutoffs established here were also initially distinct from cutoffs used to determine
direct CARES Act aid through the Coronavirus Relief Fund (CRF), through which cities and counties
above 500,000 in population were eligible for direct aid—an important consideration we return to when
interpreting effects on public sector employment.24
“Downstreaming”, whereby for example, a state or higher-level government issues on behalf
of a cash-flow managing instrumentality or political subdivision is permitted, but the extent of
downstreaming is regulated by state legislative approval. Further, the MLF established maximum
MLF borrowing caps for each issuer as 20% of each issuer’s 2017 “Own-Source General and Utility
Revenue” (OSGUR), which implicitly limits the extent of downstreaming.25 In our setting, the presence
of downstreaming will tend to attenuate any effects we find through our regression discontinuity
analysis, as ineligible issuers are more likely to be beneficiaries of downstreaming when subdivisions
do not already have direct MLF access. We thus interpret all RD estimates as a lower bound on the direct
MLF access effect in this paper.
April 27, 2020: Municipal Liquidity Facility (MLF) Population Cutoffs Expanded. Central to our empirical
strategy, on this day eligibility was expanded to cities with populations greater than 250,000, counties
with populations greater than 500,000, and multi-state entities were included as eligible issuers.26 Tenors
were also extended to allow up to 3-year maturity notes to provide maneuvering room for localities in
which Balanced Budget Requirements (which usually preclude deficit borrowing across fiscal cycles) are
statutorily amendable or flexible. Terms regarding minimum credit ratings were also established—“an
Eligible Issuer that is not a Multi-State Entity must have been rated at least BBB-/Baa3 as of April 8, 2020,
by two or more major nationally recognized statistical rating organizations (“NRSROs”). An Eligible
22 See Examination of the Municipal Liquidity Facility, 09/17/20, Congressional Oversight Committee
23 Details regarding the penalty pricing grid are shown in Appendix A.2.
24 Cities and counties with populations under 500,000 could receive CRF aid as well, but had to rely on their underlying
states to downstream aid to their localities, which is potentially politicized and less certain.
25 OSGUR caps use 2017 as a base as it reflects the latest year prior to 2020 in which the U.S. Census Bureau’s Annual Survey
of State and Local Government Finances administers a full government census (conducted every 5 years, with sampled surveys
in the interim). For a list of OSGUR caps per issuer, see Federal Reserve Municipal Facility Limits.
26 The MLF term sheet defines multi-state entity as an entity created by a compact between two or more States, approved
by the United States Congress, acting pursuant to its power under the Compact Clause of the United States Constitution MLF
Term Sheet, April 27, 2020. These include for example, authorities like the Port Authority of New York and New Jersey.
14
Issuer that is not a Multi-State Entity and that was rated at least BBB-/Baa3 as of April 8, 2020, but is
subsequently downgraded, must be rated at least BB-/Ba3 by two or more major NRSROs at the time
the Facility makes a purchase.” (MLF Term Sheet, April 27, 2020). In other words, issuers are required
to have had investment-grade ratings both prior to the pandemic and at time of issuance. Finally, this
announcement added an explicit sunset date of December 31, 2020.
Extensions: Several notable extensions were announced thereafter, including the publication of the
MLF pricing grid (May 11) and revision to the pricing grid (August 11). On June 3, the MLF was
expanded to allow state governors to specially designate up to 2 ineligible cities or counties as eligible,
as well as two revenue-bond issuers (RBIs) per state.27 The cap of governor-designated city and county
issuers varies between 0 and 2 per state depending on the number of already-eligible cities and counties,
as some small states had fewer eligible issuers according to the April 27 cutoffs.28 Like downstreaming,
to the extent that this Governor privilege is utilized when issuers do no already have direct access to the
MLF, our RD strategy estimated should be interpreted as lower bounds on the true effect. Because these
subsequent extensions were minor relative to earlier announcements, we label all activity beyond April
27 as the “post-period”, analogous to how we defined the “pre-period” prior to March 23.
3 Data Sources and Underlying Variation
3.1 Linking Trades and Primary Issuance to Census Populations
We desire a dataset that allows us to link high-frequency municipal bond trades and new primary
issuance to MLF-eligible (and ineligible) localities. Toward this end, we begin with the universe of
unique Bloomberg issuers which are sorted by type (e.g. city, county, state, school district, etc.) at the
6-digit base CUSIP level. These contain both issuers with active debt, as well as small issuers who do
not have (or never had) outstanding debt, and allow us to first flag all city and county issuers. We
then acquire and clean the universe of secondary market municipal bond trades from the Municipal
Securities Rulemaking Board (MSRB) via their Electronic Municipal Market Access (EMMA) service.
Since 1998, MSRB has required registered dealers to report all municipal bond transactions, which
include information about their 9-digit bond CUSIP (the first 6-digits of which correspond to base
CUSIP), date and time of trade, price and yield, maturity, coupon, par volume traded, total amount of
the bond, and a flag for whether the dealer bought from a customer, sold to a customer, or whether the
transaction was an inter-dealer trade. Importantly, the detailed security description has full information
27 While RBI issuer access to the MLF may be reflected in aggregate estimates of market yields, our main regression
discontinuity design is restricted to cities and counties and thus remains insulated from this designation—we therefore do
not focus on it.
28 See MLF Term Sheet, June 3, 2020 for further details.
15
on the issuer’s name and geography.
For our regression discontinuity strategy, our main analysis period is contained in calendar year
2020, however to provide an additional year of pre-trend we keep all trades occurring after January
1, 2019, and end our sample frame on November 20, 2020. After restricting our analysis to city and
county issuers, this results in 2,849,015 trades of 194,068 bonds across 7,936 unique issuers in our
MSRB-Bloomberg matched data.29 To establish issuer lending eligibility cutoffs, the MLF makes use
of two specific Census Bureau files: a 2018 population list for cities and towns, and a 2019 population list
for counties.30 These files contain detailed place (government) names and populations, however do not
carry CUSIP identifiers. We thus extensively clean MSRB issuer names to match these Census place name
lists, and are able to match 6,015 / 6,842 of MSRB city issuers and 1,921 / 1,947 of MSRB county issuers to
populations respectively. Figure 4 below shows the distribution of matched city and county issuers and
trades prior to all Federal announcements, focusing on municipalities with populations above 100,000
and cities less than 1.5 million for exposition.
29 Cities: 1,930,235 trades, 141,976 bonds, 6,015 issuers; Counties: 918,780 trades, 52,092 bonds, 1,921 issuers.
30 U.S. Census Bureau, “Annual Estimates of the Resident Population: April 1, 2010 to July 1, 2018” for cities, as of April 6,
2020; and U.S. Census Bureau, “Population, Population Change, and Estimated Components of Population Change: April 1,
2010 to July 1, 2019” for counties, as of April 6, 2020. As these files cover populations greater than 50,000, we further use U.S.
Census Bureau 2010-2019 Populations, All Places Files to fill in populations when less than 50,000. This name cleaning process
is involved, and described in detail in Appendix A.3.
16
Figure 4: Running Variable Distribution of Issuers and Trades around Lending Eligibility Cutoffs
NOTES—For exposition, cities and counties are shown for populations over 100,000; including 0 to 100,000 would
result in a large spike of small issuers which are omitted here to focus on variation around the 4/27/20 cutoff. All
data here are restricted to trades prior to March 1, 2020, to demonstrate variation prior to the onset of the pandemic
and choice of cutoffs. See text for how issuers, trades, and populations are merged together. Source: US Census
Bureau, MSRB, Bloomberg
The first thing to note about this figure is that the initial MLF eligibility cutoff established on 4/9/20,
while able to target the most traded bonds, ultimately resulted in very few eligible issuers (blue bars).
Were this cutoff to have remained in place, 24 issuers with 7,561 outstanding bonds would have been
MLF-eligible. The revision of cutoffs to their 4/27/20 levels (red bars) expanded eligibility to a total
of 203 issuers with 37,690 outstanding bonds (prior to the pandemic).31 For these reasons, we focus
all subsequent analysis on the 4/27/20 cutoffs, as any variation across the initial cutoffs would be
smooth across the new thresholds. While a formal Frandsen (2017) test (analogous to a McCrary (2008)
test for a discrete running variable (Cattaneo et al., 2018)) is provided in Section 6, the smooth mass
around the new cutoffs combined with institutional details behind the selection of 250,000 and 500,000
as cutoffs (including their apparent use of round number heuristics) also provides preliminary evidence
that cutoffs were not chosen to target specific types of issuers or anomalies in the population distribution.
31 Of all eligible MLF issuers, only Madison, WI, did not have trading bonds after Jan 1 2019 in our data. We otherwise have
fully coverage of city and county eligible issuers.
17
While restricting the data to trading bonds provides an important lens into yields, we are also
fundamentally interested in effects on new primary issuance. However bonds that are newly issued
but do not trade (or trade sparsely or with a lag relative to issuance) would not appear in the MSRB
data. For this reason, we turn to Mergent which contains the universe of municipal issuance. In
addition to the 194,068 trading bonds in our MSRB post-2019 sample, from Mergent we are able to
add an additional 9,002 bonds that are newly issued but do not trade.32 Mergent also provides key bond
characteristics, including offering amount, the source of funds and use of proceeds, coupon type (fixed,
variable, or zero), the tax status of the coupon payments, callability and first call date, insurance status
and the identity of the insurer, and pre-refunding status and timing. We discuss these variables, cleaning
procedures, and tax adjustments, in Appendix A.4.
Credit Ratings
To analyze effects by creditworthiness, we construct time-varying issuer credit ratings from ratings
data on their underlying bonds. We first acquire monthly ratings updates at the bond level from
the three major nationally recognized statistical rating organization (NRSROs): Standard and Poor’s
(S&P), Moody’s and Fitch.33 At the CUSIP level, we ascribe all trades that occur within the month
following each ratings observation their long-term, short-term and muni bond rating (when available).
We then concord all long-term, short-term, and muni-ratings—each system specific to their NRSRO—to
an aggregated S&P Ratings bin (AAA, AA, A, BBB, BB, CCC, C, D) using a custom concordance file.34
Following Boyarchenko et al. (2020), we finally construct issuer plurality ratings within issuer-month,
equal to the most common aggregated bond rating across NRSROs and CUSIPs that month. This allows
us to subset on pre-pandemic fixed issuer ratings when implementing heterogeneous specifications. In
Figure 5 below, we show the resulting distribution of plurality ratings (at the trade-level) when fixing
the rating to January (or February) 2020, and when letting the plurality rating vary by month.
32 Among city and county issuers, non-traded bonds are generally constrained to localities with populations less than 25,000,
and therefore newly issued bonds are largely irrelevant to our analysis of yields. We otherwise, are unable to match 25% of
Mergent non-trading bonds to Census populations due to mismatches in Mergent issuer names and Census issuer names.
33 These are assembled via Bloomberg.
34 See Appendix A.5 for further details on these concordances and the construction of plurality ratings.
18
Figure 5: Plurality Ratings Distribution for Cities and Counties
(a) All Cities and Counties: (b) Cities and Counties within 100k of Cutoff:
NOTES—Figure shows distributions of trades according to monthly plurality issuer ratings from January 1, 2019
to November 20, 2020. See text for details. Source: MSRB, S&P, Moody’s, Fitch
This figure shows that the ratings distribution is both heavily skewed toward high-credit issuers, and
relative stable over time. In panel (b) we show the distribution for an arbitrary bandwidth of 100,000
around city and county cutoffs, to show stability in the distribution to this sub-sample (used to highlight
the key variation in the regression discontinuity design in the next sub-section). To the extent that
there are monthly credit downgrades that occur differentially after the pandemic, or for MLF-eligible
versus non-eligible issuers, we use disaggregated ratings and the bond level. This allows us to ask
whether the probability that a bond was downgraded relative to the prior month changed overall, and
heterogeneously by baseline plurality ratings (for example within January 2020 BBB’s). Generally, we
are able to match 96.3% of trading bonds to a monthly plurality rating, where 3.7% of the unmatched
reflect the inability to find a plurality when ratings are split.
3.2 Underlying Variation in Yields
We now turn to highlighting the underlying variation in our matched sample. In our main regression
discontinuity design specification, we choose the running variable’s window of analysis using an
optimal bandwidth selection procedure (following Calonico et al. (2014)) which takes choice and
publication bias out of the econometrician’s hands. In this section, we first show some of the key
variation underlying our design using an intuitive symmetric population bandwidth of 100,000 below
(ineligible) and 100,000 above (eligible) MLF population cutoffs. In Figure 6, we show unconditional
weekly mean yields (i.e. without covariate adjustments) separately by issuers narrowly eligible for MLF
(blue dashed series), and similar-sized issuers that narrowly miss MLF eligibility (red solid line).
19
Figure 6: Mean Yields within 100k Population of MLF Eligibility Cutoffs
By geography:
(a) Cities: (b) Counties:
By credit worthiness:
(c) High-Rated (AAA & AA): (d) Low-Rated (A & BBB):
NOTES—Figure shows mean weekly yields (pooled over buyer and seller prices) for eligible issuers with
cutoff-relative populations between 0 and 100,000 inclusively (blue dashed series), and issuers with cutoff-relative
populations greater than or equal to -100,000 and less than 0 (red solid series). Trades between announcements are
pooled into a single period beginning on the announcement day. See text for sample restrictions and definitions.
Source: MSRB, S&P, Moody’s, Fitch
Panels (a) and (b) show city and county yields exhibited relatively parallel pretrends that rose
together during the liquidity crisis in the run up to the first Federal intervention on March 23rd (left
black dashed line).35 Cities and counties continued to track each other throughout the initial MLF
announcement (middle gray dashed line) until the announcement of the April 27 cutoffs—the main
focus of this design.36 Panel (a) shows investor-perceived measures of MLF access (yields) did not
differentially materialize in cities after the third announcement’s cutoffs were mandated. While there
35 This is a necessary condition for any regression discontinuity design as the bandwidth approaches 0 in the limit; here we
already begin to see observational equivalence (in the dependent variable) with an arbitrary symmetric cutoff of 100,000.
36 To ensure bin means do not overlap announcements, we mean-collapse all yields that fall within inter-announcement
intervals to a single observation centered at each interval’s midpoint (inclusive of the Monday of the each announcement).
20
appears to be mild visual evidence that narrowly ineligible county bonds began trading at lower prices
(higher yields) than eligible counties after the third announcement, this difference in not statistically
significant in formal regressions. Both plots show full resumption to pre-crisis levels in the long run.
However, turning to panels (c) and (d), the main results of the paper become apparent from simply
inspecting the path of these means across the ratings distribution. In these panels and subsequent
analyses, we pool the two highest and two lowest investment-grade issuer plurality ratings from January
2020 (fixing issuer ratings at their pre-crisis levels) for statistical power—a choice motivated by the sparse
BBB mass shown in panel (b) of Figure 5. While high-rated bonds share the same pattern as the overall
market, among lower-rated bonds, a strong wedge begins to emerge exactly when the new cutoffs are
made binding, immediately after the third announcement. Importantly, the timing of the yield wedge
(exactly in the week the revision was announced) also minimizes concerns that chosen population cutoffs
may have been used for other COVID-related policies, which would have appeared differentially in
the pretrend before April 27. Of greatest concern, the March 27 CARES Act Coronavirus Relief Fund
(CRF) also used a direct aid cutoff of 500,000 for both cities and counties—however both panel (b) which
contains counties that were eligible for both policies, and the main effects in panel (d), provide initial
evidence that yields did not respond to direct CARES aid a month earlier, instead only responding to the
MLF cutoff expansion.37
Analyzing the levels of these means, low-rated MLF-ineligible bonds (red series) remained
significantly distressed beyond the last Federal intervention, in line with the aggregate BBB municipal
market trend initially presented in Figure 1. By contrast, low-rated MLF-eligible bonds appear to recover
fully to pre-crisis levels, mimicking the behavior of high-rated bonds when supported by the MLF.38
In some weeks, this wedge is as large as 100 basis points—roughly half the pre-crisis spread level. The
question of how to interpret these differential effects that are only present among low-rated bonds, forms
the basis of our formal analysis, and is discussed in Section 4.
Sample Restrictions
The above plots apply three sample restrictions, which are also applied throughout the estimation
section: (1) we two-tail winsorize all yields at the 1% level; (2) we drop all yields with likely classical
37 We probe this initial evidence more formally in subsequent robustness tests below.
38 This pattern also emerges strongly when looking separately at A and BBB categories, as we show in additional results in
Figure A.4 of Appendix A.7. We also examine whether selection on composition can explain these results in Figure A.8, which
shows that while there is some evidence that revenue bonds are traded disproportionately following the announcement, this
pattern is not sustained throughout the series. Furthermore, these patterns are not driven by refinancing: among the bonds
trading in the 2020 A and BBB sample within 100,000 of the cutoff, only 4 were redeemed after the April 27 announcement, all
of which were advanced refunding deals among MLF-ineligible issuers.
21
measurement error (prices less than 50, and greater than 150, following Green et al. (2010));39 (3) we drop
any secondary market trades occurring within 90 days of primary issuance following Schwert (2017).40
After imposing these restrictions, the pooled low-ratings sample (the smallest in our analysis and thus
the one warranting the most power concerns) is comprised of 759 issuers, 7,248 bonds, and 94,849 trades
in the post-period; with 4.75% of bonds falling with 100,000 population above the cutoff, and 3.53%
within 100,000 below the cutoff.41
3.3 Public Sector Employment Data
We leverage an additional source to estimate effects on real-economy outcomes: local public sector
employment by county-month and sector at eligible and non-eligible localities.
QCEW Government Employment data: We use the May 26, 2021 revised release of government
employment data from the U.S. Census Bureau Quarterly Census of Employment and Wages (QCEW),
which includes a monthly stock of all workers that were employed on the 12th day of the month through
the end of 2020Q4 (through December 2020). The QCEW is based on ES-202 unemployment insurance
filings at the state level, required for filing payroll taxes for federal UI-covered workers, so our sample
requires a minimum level of part-time work for an employee to be included. This data covers roughly
90% of U.S. employees, excluding self-employed workers, some agricultural workers, and informal
workers, and roughly 96% of state and local government workers (BLS-QCEW).42 The QCEW is unique
in its ability to provide a census of employees at a relatively granular sector-by-geography resolution.
The most disaggregated geography in this data is at the county level, however public sector employees
are also broken out by level of government: we use Local Government Employees (Ownership Title =
3) employed in Total, All Industries (NAICS = 10) as our preferred measure, which excludes state and
federal employees but aggregates city and county employees at the county level. For roughly 67% of
the data, sector-specific components of government employment are readily available, and allow us to
separately estimate effects for goods-producing (NAICS = 101) and service-providing (NAICS = 102)
public employees, the latter of which is largely comprised of Education and Health Services employees
(NAICS = 1025).43
39 Recall that prices at par, for the most part, vary closely around 100 at time of initial issuance.
40 The results in Figure 6 are nearly identical without these restrictions.
41 In Appendix A.6, we further enumerate the list of 43 A and BBB city and county issuers that fall within 100,000 in
population of the cutoff, along with the number of bonds issued for each.
42 Contractors are also covered by the QCEW (BLS), and reflect about 10% of local public sector employment (the sample
studied in this paper), and include goods-producing employees. See Hyman (2018) for an explanation of sample coverage
using similar data.
43 We are able to confirm for this subset, that goods and services sector sub-components add up to aggregate employment
totals, and thus consider these reliable. Cells that do not add up are withheld “so as to protect the identifiable information
of respondents”, and coded to missing in QCEW data as a small cell disclosure protection (https://www.bls.gov/cew/
questions-and-answers.htm question 9).
22
4 Empirical Framework
We proceed with two complementary empirical strategies: a regression discontinuity (RD) design to
estimate MLF access effects, and a spread decomposition approach to support our proposed mechanism
hypothesis and generalize to the broader market.
4.1 Regression Discontinuity Design with MLF-Eligible Populations
We estimate the option value of MLF access using a pooled regression discontinuity strategy, analyzing
effects in two distinct periods: the pre-period (prior to March 23, 2020) and the post-period (after April
27, 2020), corresponding to pre-crisis or “placebo” and post-cutoff revision or “treatment” groups.44
Yn(bi)t = α + β t ∗ 1( pop ≥ cuto f f )i + γt ∗ ( pop − cuto f f )i (1)
+ δt ∗ 1( pop ≥ cuto f f )i ( pop − cuto f f )i + Xbit + ε n(bi)t
Here, we track outcome Y ∈ {Yields, 1(Primary Issuance), 1(Credit Downgrade), Public Sector
Employment}. When the outcome is yields, we measure trade n of bond b from issuer i in period t.
1( pop ≥ cuto f f ) is an indicator variable that takes a value of 1 if the running variable (population
relative to cutoff) is greater than or equal to zero. We use “relative population” as the running variable to
be able to stack cities and counties with different cutoffs together in one specification. The γ and δ terms
estimate separate polynomial slopes on each side of the cutoff, and capture the parametric relationship
between city/county size and the outcome variable. α estimates the cutoff-intercept of the γ term’s
slope from the left-hand side, and has the convenient interpretation of representing the control group
(MLF-ineligible) mean close to the cutoff. β t is the parameter of interest, and estimates the difference in
intercepts between the left polynomial and right polynomial at the cutoff, or the jump in the regression
function at the cutoff.45
We follow Calonico et al. (2014) and Gray et al. (2020), in using a data-driven optimal bandwidth
selection procedure to select asymmetric bandwidths on either side of the cutoff for estimating each
polynomial, which subsequently helps determine the parameter of interest.46 The procedure chooses
bandwidth boundaries that minimize the integrated mean-squared error (IMSE) of the regression, which
is linearly separable in bias and variance terms that are traded off in the bandwidth selection (smaller
44 In Figure A.5 of Appendix A.7, we also provide estimates from a dynamic monthly RD specification.
45 For continuous running variables, this builds on a well known statement that if the average potential outcomes are
continuous functions of the running variable at the cutoff, the difference between the limits of the observed outcomes of two
groups (as the score converges to the cutoff) is in fact the average treatment effect Hahn et al. (2001).
46 This method takes one choice parameter—bandwidth—out of the econometrician’s hands, thus minimizing susceptibility
to publication bias and “p-hacking”.
23
bandwidths are less biased but higher variance; larger bandwidths are more precise but also more
biased). We use a non-parametric first-order polynomial (hence the linear terms) with an asymmetric
triangular kernel that weights observations closer to the cutoff with values closer to 1, and diminishing
weights moving away from the cutoff (and weight=0 beyond the bandwidth boundary).47 In practice,
the choice of kernel has little sway over regression results, while the choice of bandwidth can be
massively influential (Cattaneo et al. (2019a)). While a consistent estimate of β t does not require
covariates to be identified (and in fact, should be robust to estimation without covariates), in small
samples, the precision of estimates can be improved by their inclusion. We thus include the X vector
to account for mostly time-invariant bond and issuer characteristics in subsequent regressions, however
all results are robust to their exclusion. Lastly, we conservatively cluster standard errors on the running
variable (relative population) so that inference is drawn from between-issuer differences rather than
within-issuer—consistent with recommendations for a discrete running variable (Frandsen, 2017).
Importantly, we also estimate Equation 1 separately for the four pre-crisis plurality credit ratings
types of issuers (AAA, AA, A and BBB), which we interpret as a reduced form test of risk-sharing. As
discussed earlier, in our main estimation, we pool the two highest and two lowest investment-grade
issuer plurality ratings from January 2020 for statistical power. Our hypothesis is that if the Federal
sector directly shares credit-downgrade or credit-default risk, one would expect lower rated eligible and
non-eligible issuers to have stronger price spreads due to comprising a higher share of bonds on the
default margin. If instead there are neutral effects, this direct access most likely reflects an “added MLF
liquidity effect” beyond what is already happening in the aggregate.
4.1.1 Identifying Assumptions and Balance Test
The key identifying assumption of the RD is that potential outcomes are smooth across population
relative to MLF eligibility cutoffs, absent the cutoff announcement itself.48 Any selection on the running
variable could violate this by breaking the associated “no manipulation” or “no sorting” requirements,
which ensure that the RD is locally as good as random. As we showed, this is unlikely to be problematic
in our setting. However, similar to randomized controlled trials, this identifying assumption generally
has a natural falsification test (should pre-treatment data be available) that helps support the validity of
the assumption: estimating the RD on baseline data prior to the experiment itself.
In our context, we have collected many months of a pre-period placebo outcome data (prior to March
23, 2020), in which we can formally test this assumption on our trade-level dataset. In Table 1, we
47 We provide the implied kernel weights from the IMSE-optimal bandwidth selection procedure in Figure A.6 of Appendix
A.7. The order of polynomial is chosen to best fit the underlying data.
48 For a discrete running variable, the “local continuity” assumption is softened to “local randomization”.
24
estimate Equation 1 for the pooled city and county sample in the period from Jan 1, 2020 to March
23, 2020, where each row reflects a separate regression in which a new optimal bandwidth is selected
depending on the outcome variable, thus producing different observation counts per variable.
Table 1: RD Balance Table in Placebo Period
Discontinuity Standard Error Control Mean N (IMSE-bwdth)
Coupon Rate (b.p.) -23.32 17.36 435.32 99,376
Security Price (per 100 par) -1.98* 1.11 109.95 111,063
Current Yield (b.p.) -6.12 16.20 185.81 70,567
∆ Yield (Feb20-Jan20) -0.03 0.05 -0.10 66,117
∆ Yield YoY (Jan20-Jan19) -0.23 0.20 -0.94 54,748
∆ Yield YoY (Feb20-Feb19) 0.04 0.11 -1.01 53,251
Amount Outstanding (MM) -18.84 190.89 473.60 90,163
Maturity Size (MM) 11.86 268.45 707.74 89,923
Tenor of Bond (Years) 0.36 0.90 12.88 110,907
Remaining Duration of Bond (Years) -0.19 0.85 8.26 97,529
Market Share of Issuer 0.03 0.10 0.18 92,770
Number of Securities by Issuer -29.24 43.26 227.60 129,779
Par Traded of Bond (1000s) 37.78 35.76 92.27 95,764
S&P Ratings (1-7 scale) 0.08 0.14 5.60 89,886
Moodyś Ratings (1-7 scale) 0.13 0.18 5.72 87,394
Fitch Ratings (1-7 scale) -0.03 0.17 5.69 75,032
Time of Day of Trade (minute) 10.67** 4.86 768.28 101,011
NOTES—Table presents balance tests of covariates for MSRB active trades during the pre-period for the pooled
sample. Each row corresponds to a separate regression with that characteristic as the dependent variable. The
discontinuity measures the jump in the regression function at population eligibility 0 (relative to cutoff). The
Control Mean denotes the mean of that characteristic immediately to the left of relative population 0. Each
regression uses IMSE-optimal bandwidths calculated separately for each side of the cutoff and for each outcome,
and a triangular kernel to weight observations. Sample sizes vary depending on the bandwidth used. See
Appendix A.4 for further details on variable definitions and construction. Standard errors are clustered by
population relative to the cutoff (the running variable). *** p≤0.01, ** p≤0.05, * p≤0.1. Source: MSRB, Bloomberg,
S&P, Moody’s, Fitch
Each regression is estimated unconditionally, without adding covariates on the right-hand side.
“Discontinuity” and “Control Mean” columns correspond to β and α respectively from Equation 1.49
Among the dependent variables listed, there are only few cases in which a significant break is detected
in the placebo sample. When they are detected, the control mean suggests that they are not economically
meaningful or large in magnitude, and thus simply a result of randomization (sampling) error.
Furthermore, estimates on the important yield variables, which include both a month-to-month and
year-on-year trend variable, are particularly small relative to their control means.50 While randomization
errors are more likely to occur within smaller samples, such as estimates within lower-rated bins, the
combination of balance in the placebo period and relatively parallel pretrends in dependent variables
49 A full set of summary statistics can be found in Table A.5 of Appendix A.7.
50 For more details on the how the remaining variables are constructed, see Appendix A.4.
25
shown earlier, suggests that the local randomization assumptions hold in this setting.
4.1.2 Differenced RD Modification for Employment Effects
We also desire to estimate the effects of MLF eligibility and related CARES Act aid on city and county
public employment outcomes in our RD framework. Recall that MLF eligibility could directly support
the retention of employees by allowing the matching of cash in- and outflows. In addition, to the
extent that MLF eligibility enhances an issuer’s ability to refund outstanding long term debt, this could
reduce debt service costs, freeing up cash flow that could be used to provide services and maintain
payroll. We face, however, a challenge in addressing this very important issue. Data limitations
only allow us to observe local public employment combined for city and county employees at the
county-month level. That is, while the QCEW provides exceptional coverage of employment and
breakdowns by sector, it does not decompose total local public employment into its city and county
sub-components—consequently, any effort to estimate RD effects for counties could be made difficult by
the possibility that an untreated county’s public employment to the left of the county population cutoff
is partially covered by an MLF-eligible city; symmetrically, an untreated city could be covered by an
MLF-eligible county. Both of these cases would attenuate relative employment effects toward 0.
For these reasons, we opt for a strategy comparing combined city and county eligible counties on the
right of the cutoff, with “neither-eligible” counties to the left of the cutoff, and propose a novel adaption
in the spirit of difference-in-discontinuity designs to difference out any unintended selection concerns
resulting from this measurement strategy. We first pre-sort cities and counties into four cases: (a) the
county itself is the only MLF-eligible issuer within the entities spanned by the county; (b) only 1 city is
MLF-eligible within the county, while the county itself is ineligible; (c) both the county and one of its
underlying cities are MLF-eligible; (d) neither the county nor any of its contained cities are MLF-eligible.
We show representative maps for cases (a), (b) and (c) in Figure 7 below.
26
Figure 7: Differenced RD Design with QCEW County-Level Employment: Three Treatment Cases
(a) County-Only: Salt Lake County, UT (b) City-Only: Lincoln, NE (c) Both: K.C. & Jackson County, MO
NOTES—In panel (a), Salt Lake County, UT, is eligible while none of its overlapping cities (nor unincorporated
areas) is eligible; in panel (b), Lincoln, NE is eligible, but none of the other cities nor the county containing it
(Lancaster County) are eligible; in panel (c), both Kansas City, MO, and Jackson County, MO, are eligible, while
the remaining 3 counties spanned by Kansas City would be considered type (b), city-eligible only.
In our preferred strategy to estimate employment effects, we combine all case (a) “county-only”
types (spanning 59/119 MLF-eligible counties) with case (c) “double-eligible” types (spanning 60/119
eligible counties) on the right of the cutoff of the county running variable, and compare these with case
(d) “neither-eligible” types to the left of the cutoff along the same running variable.51 The modified RD
identification assumption is that potential outcomes are smooth around each running variable’s modified
sample. To the extent that these pre-sorted samples introduce further selection concerns, and to address
the potential problem that any RD randomization error could magnify level differences emanating from
differently sized geographies around the cutoff in these modified samples, our preferred specifications
consider the first-difference change and percent change in employment (year-on-year) rather than its
level. Year-on-year changes in employment in a given month should difference out any aggregation
errors arising from this sorting procedure, and as county employment levels have a long right tail,
focusing on changes also helps reduce noise in these estimates.
In all employment regressions, we depart from our IMSE-optimal bandwidth selection procedure
and instead use a fixed bandwidth due to the much smaller number of observations—an N between
700 and 900 (whereas yields RDs are estimated from tens and sometimes hundreds of thousands of
observations). We choose a fixed bandwidth of 400,000 below the cutoff, and 600,000 above the cutoff,
51 In Appendix A.7, we also separately compare case (b) cities (spanning 21/86 eligible cities) against case (d) types along
the city running variable (which requires constructing city employment by calculating the employment weight of each county
spanned by the city). This sample has the added appeal that the city MLF eligibility cutoff (250,000) is distinct from the
CARES eligibility cutoff (500,000), however power calculations in the Appendix show we are unable to detect large effect sizes.
Furthermore, estimating effects on the city running variable also requires strong assumptions to assign county employment
weights to multiple untreated cities within a given county.
27
allowing us to take advantage of a full window size that spans localities of 1 million in population
(between 100,000 and 1.1 million). As before, we employ a triangular kernel that weights observations
near the cutoff close to 1, and observations at the bandwidth boundary equal to 0. As we did for
yields, we two-tail winsorize employment values at the 0.1% level prior to taking first differences. For
consistency with yields results, we include state fixed effects in some regressions (and month fixed effects
when the outcome is not year-on-year first differenced), however all employment effects are robust to
being estimated unconditionally without covariates.
5 Results
We first present results from our regression discontinuity strategy on the effects of the MLF on secondary
market yields, primary issuance, and real economy outcomes.
5.1 RD Effects on Secondary Market Yields
Table 2 presents our main results on the investor-perceived option value of access to the MLF, estimated
from secondary market municipal bond yields (in basis points).
Table 2: RD Estimates of MLF Access on Secondary Market Yields
Discontinuity Standard Error Control Mean N (IMSE-bwdth)
a. Pooled Post:
Overall Yield -19.42 19.47 156.71 189,076
City Only -27.91 25.48 171.75 92,349
County Only -16.04 24.11 134.83 54,574
High-Rated -1.75 7.80 124.99 179,380
Low-Rated -75.43** 34.11 307.69 37,977
b. Pooled Pre (Placebo):
Overall Yield -13.26 12.15 194.07 70,567
City Only -9.34 12.14 196.35 32,499
County Only -21.61 19.17 191.88 28,325
High-Rated -6.09 7.73 177.31 67,350
Low-Rated -25.14 21.64 263.29 12,576
NOTES—Table presents RD estimates of current yields (in basis points) for MSRB-active trades during each sample
period. Each row corresponds to a separate regression with that characteristic as the dependent variable. The
discontinuity measures the jump in the regression function at population eligibility 0 (relative to cutoff). The
Control Mean denotes the mean of that characteristic immediately to the left of relative population 0. Each
regression uses IMSE-optimal bandwidths calculated separately for each side of the cutoff and for each outcome,
and a triangular kernel to weight observations. Sample sizes vary depending on the bandwidth used. State and
calendar month fixed effects are included in all regressions. Standard errors are clustered by population relative
to the cutoff (the running variable). See text for further sample restrictions. *** p≤0.01, ** p≤0.05, * p≤0.1.
Panel (a) pools all trades post-April 27 into one treatment sample, whereas panel (b) pools all
28
pre-March 23 observations into one placebo sample (starting from January 1, 2020). Each row
representatives a different sub-sample of issuers and separate regression, as discussed above. As before,
the “discontinuity” and “control mean” columns correspond to β and α from Equation 1 respectively.
In this regression table, we implement the sampling restrictions for yields discussed in Section 3, and
include calendar month fixed effects to absorb time series variation in overall levels, and state fixed
effects to reduce variability from differences in exemption rules and budget balance requirements (which
can limit downstreaming) across states.52
Consistent with the event study plots, we fail to detect a statistically significant differential effect
between eligible and ineligible issuers in the post-period overall, nor by city or county. The highest
rated issuers appear to also be unaffected by the announcement of MLF eligibility.53 Moving down the
ratings gradient however, we estimate a strong statistically significant yield spread for low-rated issuers.
The point estimate suggests that narrowly MLF-eligible issuer bonds trade, on average, 75 basis points
lower (i.e. at a higher price) than observationally equivalent issuers that narrowly miss the cutoff. This
wedge represents about 24% to 28% of baseline yields (depending on whether one benchmarks to the
pre-crisis (263.29) or post-crisis (307.69) period respectively), a magnitude that closely corresponds to
the overall municipal market wedge between BBB yields and higher-rated issuers as shown initially in
Figure 1. In fact, when estimated separately by BBB and A, effects among BBB-rated issuers are even
stronger than this average (see additional results in Figure A.4 of Appendix A.7).
It is worth highlighting that including state fixed effects in our main specification also implicitly
tax-adjusts yield estimates—since the above table is restricted to 2020, state fixed effects would account
for any differential state tax rates and exemption rules on muni income accrued to the marginal investor
residing in each state, who is presumed to take advantage of doubly-exempt bonds (i.e. muni interest
income that is exempt from federal and state tax liabilities). In Section 6.3, we report the sensitivity
of our RD results to directly adjusting tax-exempt bonds using NBER-TAXSIM effective rates for a
representative high-wealth household investor in each state, as well as excluding state and month fixed
effects, all of which show our results are qualitatively robust to excluding all covariates and do not rely
on any specific tax adjustment method.54
Encouragingly, for all subgroups, estimates in the pre-period are close to zero. This suggests that
balance is achieved even among these smaller sample sizes using only a parsimonious number of
52 State fixed effects are estimated using all data within the optimal bandwidth, spanning close to 759 issuers (the total
number in the combined A and BBB group.)
53 In regressions by ratings bin, we pool cities and counties together for statistical power.
54 NBER-TAXSIM provides these rates net of local cross-deductibility rules, including mortgage interest deductions. The
latest rates provided are for 2018, which we assume are the effective rates salient in 2020. See 2018 “Wages Federal Rate” for
the effective rate applied to federal-only exempt bonds, and “Wages Total Rate” for the sum of federal and state effective tax
rates applied to each state’s underlying bonds (https://users.nber.org/~taxsim/state-rates/maxrate.html).
29
standard controls (state and month fixed effects). To explore the precision and sensitivity of our preferred
estimates transparently, below we show RD scatter plots associated with high- and low-rated issuers.
Figure 8: RD Plots of MLF Access Effect on Yields by Credit Worthiness
NOTES—Plots show regression slopes and intercepts from Equation 1 in the post period, overlaid on top of equally
spaced pre-binned outcome data with a bin size of 20 (x-axis in thousands). Plots are shown over the optimal
bandwidth selected using the IMSE-procedure, which produces (potentially) asymmetric optimal bandwidth
boundaries for each sample. Plots correspond to Table 2, which includes state fixed effects as controls. Plot thus
residualizes all yields by state-fixed effects (added back to their overall mean) prior to mean-collapsing by bin.
Here, we begin to see a pattern of which issuer types investors appear most responsive to across
the relative population distribution (the running variable). Among high-rated bonds, yields are neutral
across city (and county) size distributions. This neutrality is preserved for low-rated issuers that are
MLF-eligible (flat slope), yet for the ineligible issuers, an upward-sloping relationship appears in which
larger locations have higher yields, but only up to the cutoff. These estimates remain nearly identical
when controlling for bond type (general obligation versus revenue bond), tenor length, remaining bond
duration, as well as trade week, day of week, maturity size, and amount outstanding.55 To the extent
that there are concerns that the RD is picking up underlying volatility beyond these controls, we note
that RD polynomial terms on either side of the cutoff account for any remaining differential volatility by
relative population. This is further confirmed by placebo RD plots in Section 6 which do not show any
strong pre-existing pattern in volatility.
We interpret these results as suggestive of a setting in which pre-existing uncertainty in the pricing
environment for low-rated municipal issuers (those with more bonds on the margin of default) may have
been amplified by the pandemic. This credit risk seems to have been priced differentially by investors,
depending on whether issuers had the ability to borrow from the Federal sector as a last resort lender.
In the following section, we then ask whether such perceptions also impacted new debt issuance.
55 See sensitivity table shown in Section 6.3.
30
5.2 RD Effects on Primary Issuance
In Figure 9 below, we first visually inspect whether investor perceptions which created a wedge in
secondary market yields also induced additional new primary issuance of municipal notes or bonds,
differentially for MLF-eligible issuers. Combining all new issuance from MSRB and Mergent data, we
first show graphically the cumulative stock of bonds that were newly issued (defined here as having a
first offering during calendar year 2020), by each week of the 2020 calendar year.56
Figure 9: New Primary Issuance within 100k Population of MLF Eligibility Cutoffs
(a) Cumulative New Issuance, All Ratings (b) Cumulative New Issuance, Low-Rated (A & BBB)
NOTES—Plots show new primary issuance as cumulative counts of newly issued bonds by MLF-eligible and
ineligible issuers within a symmetric 100,000 population bandwidth. See text for further details. Source: MSRB,
Mergent, Bloomberg
Panel (a) shows that issuers of all ratings (overall mean) within the symmetric bandwidth above and
below the pooled cutoff shared roughly equivalent trends in new issuance, with a slightly higher level
among lower population issuers due to the greater density of cities and counties of smaller populations
versus larger populations. While overall issuance does appear to converge later on in September (where
the two series intersect), this is not sustained as a strong pattern in the long run. By contrast, turning to
low-rated issuers whose bonds we confirmed were trading at higher prices after the MLF cutoffs were
revised in late April, we see a different pattern. First, the baseline level of new issuance in panel (b) is
close to zero from January to July of 2020 in both samples due to the high inherent distress levels of these
issuers, with the exception of one issuer above the cutoff that issued a series of differently-maturing
bonds prior to the pandemic. In July, we observe bonds narrowly above the cutoff beginning to issue
sooner, followed by a step function pattern of new issuances throughout 2020. The deferred timing of this
issuance (in July) relative to the immediately binding effects on yields, may be linked to the beginning
56 We choose a cumulative approach due to the lumpy nature and sparsity of primary issuance, however also formally test
the probability that a bond is newly issued separately in the pre- and post-MLF periods below.
31
of fiscal budget cycles, or coincide with the deferred IRS tax filing deadline of July 15 which may have
revealed a clearer picture of municipal revenue positions that put new issuance into motion.57
Importantly, only 5 low-rated city and county governments (within the 100k bandwidth) issued new
bonds after the MLF cutoffs were announced, 4 issuers (on a denominator of 23) above the cutoff and 1
issuer (on a denominator of 20 issuers) below the cutoff (see Appendix A.6 for denominators). With the
caveat that this does not provide bountiful variation to pick out a small signal from the noise, we now
show the formal RD estimation associated with the probability that a bond was ever newly issued after
(and before) the MLF cutoffs were announced, as well as the intensive margin amount of issuance. To
do this we collapse each CUSIP (bond or note) into a single post- and pre-MLF period observation, and
assign each bond a value of 1 if it was newly issued during that period, and 0 otherwise. Here, we depart
from optimal bandwidths due to the limited size of the collapsed dataset, and show results without
covariates for transparency. Each regression uses a fixed bandwidth of 400,000 below and 600,000 above
the cutoff, allowing us to take advantage of a full window size that spans localities of 1 million in
population (between 100,000 and 1.1 million), and a triangular kernel to weight observations close to
the cutoff with weight=1, and closer to the bandwidth boundary with weight=0.
Table 3: RD Estimates of MLF Access on New Primary Issuance
Discontinuity Standard Error Control Mean N (Fixed-bwdth)
a. Pooled Post:
Prob(New Issuance), Overall (27apr-20nov) 0.08** 0.03 0.10 89,882
Prob(New Issuance), A & BBB (27apr-20nov) 0.22** 0.11 -0.06 8,190
Total Issuance (MM), Overall (27apr-20nov) 0.76 25 82 89,882
Total Issuance (MM), A & BBB (27apr-20nov) 19 46 43 8,190
b. Pooled Pre (Placebo):
Prob(New Issuance), Overall (01jan-23mar) 0.07** 0.03 0.02 45,108
Prob(New Issuance), A & BBB (01jan-23mar) 0.08 0.08 -0.07 3,901
Total Issuance (MM), Overall (01jan-23mar) 24 27 26 45,108
Total Issuance (MM), A & BBB (01jan-23mar) 8.60 7.50 2.30 3,901
NOTES—Table presents RD estimates of the probability of new primary issuance and total amount of new issuance
(millions) in each period. Each row corresponds to a separate regression with that characteristic as the dependent
variable. The discontinuity measures the jump in the regression function at population eligibility 0 (relative to
cutoff). The Control Mean denotes the mean of that characteristic immediately to the left of relative population
0, which can be negative due to the projected RD polynomial. Sample sizes vary depending on the bandwidth
used. Standard errors are clustered by population relative to the cutoff (the running variable). See text for further
sample restrictions. *** p≤0.01, ** p≤0.05, * p≤0.1.
Table 3 shows that the probability a bond is issued increases by 8 percentage points (on a baseline
share of 10 percent), which is largely driven by an increase of 22 percentage points among low-rated
bonds. Due to the sparse nature of primary issuance, we do not have ample variation to disentangle
57 To rule out seasonal mean reversion in primary issuance as a key driver of these results, we also report the distribution of
2019 new issuance as a benchmark expansion year in Figure A.7 of Appendix A.7, which does not provide any evidence that
seasonal mean reversion is a key factor.
32
these effects completely from differential issuance in the placebo period—indeed, in panel (b) larger
municipalities are 7 percentage points more likely to issue in the pre-period relative to marginally
smaller ones. Thus, rather than interpreting these point estimates directly, we take these (along with
the larger coefficients on total issuance for lower rated bonds) as qualitative evidence that having MLF
optionality encouraged primary issuance, and investors likely priced this ability to issue in secondary
markets (especially among low rated bonds, as shown previously).
5.3 Differenced RD Effects on Public Sector Employment
We next turn to effects on local public sector employment using the differenced RD modification strategy
discussed above. In Table 4 below, we combine all case (a) “county-only” and case (c) “double-eligible”
types (spanning 60/119 eligible counties) on the right of the cutoff of the county running variable, and
compare these with case (d) “neither-eligible” types to the left of the cutoff along the same running
variable. Here again, each row represents a separate RD regression. As discussed, unlike our yields
analysis, here our preferred outcome variable is differenced year-on-year such that post-period results
reflect pooled annual changes in county local government employment for May and June (between
2019 and 2020), while the placebo shows the same effects for differenced January and February
pooled (columns (3) and (4)). As described previously, we estimate effects separately for goods- and
service-providing public sector employees, however we can only do so for the 67% of the sample in
which these sector breakdowns are reliably available, which results in different observation counts.
33
Table 4: RD Estimates of MLF Access on Public Sector Employment
Emp. Emp. ∆ Emp. ∆ Emp. % ∆ Emp. % ∆ Emp. N
(1) (2) (3) (4) (5) (6) (fixed-bwdth)
a. Pooled Post:
Overall Employment -477 323 325 297 1.19 1.18 945
(1,016) (1,854) (239) (223) (0.96) (0.83)
– Goods Employment -42 -49 1 2 2.61 3.93 248
(63) (37) (5) (5) (3.85) (4.27)
– Services Employment -412 -666 422* 517** 1.61 1.69** 711
(1,134) (2,001) (238) (242) (1.00) (0.85)
b. Pooled Pre (Placebo):
Overall Employment -828 189 53 58 0.23 0.26 946
(1,042) (1,995) (84) (82) (0.41) (0.37)
– Goods Employment -44 -51 -1 -1 -0.38 0.51 248
(64) (38) (3) (3) (2.23) (2.76)
– Services Employment -762 -896 41 26 0.10 0.04 712
(1,128) (2,188) (98) (93) (0.50) (0.41)
Month FEs X
State FEs X X X
Control Mean (post): Overall Employment 18,835 13,346 -1,717 -1,259 -8.06 -8.13
Control Mean (post): Goods Employment 162 127 -7 -5 -6.44 -7.16
Control Mean (post): Services Employment 18,506 14,054 -1,674 -1,349 -7.96 -8.58
NOTES—Table presents RD estimates of employment measure in column header and sample period. Each row
corresponds to a separate regression with that characteristic as the dependent variable. The discontinuity measures
the jump in the regression function at population eligibility 0 (relative to cutoff). The Control Mean denotes the
mean of that characteristic immediately to the left of relative population 0. Each regression uses a fixed bandwidth
with a triangular kernel to weight observations (see Section 4 for details). Percents in columns (5) and (6) range
from 0 to 100. Standard errors are conservatively clustered by population relative to the cutoff (the running
variable); as such, inference is drawn across unique issuers. *** p≤0.01, ** p≤0.05, * p≤0.1.
We begin our interpretation by analyzing employment effects in levels in columns (1) and
(2). Notably, while we fail to detect statistically significant MLF effects in levels, employment is
highly volatile in the pre-crisis (placebo) period. Importantly, the control mean in these columns
(marginally-ineligible counties) indicates our sample counties initially had roughly 18,835 local
government employees on average—heavily skewed to the right by large counties.58 The small effect
sizes contrasted with large baseline means also suggest that any effects on levels are likely estimated
with noise. Given this, in conjunction with our main selection concern that subsetting counties to isolate
precise employment effects may generate unintended imbalances in baseline characteristics, we turn
to using year-on-year differences in our preferred specification in column (3). Here, the unconditional
control group shows counties experienced an average annual decline of roughly 1,717 local public sector
employees in May and June of 2020 (relative to the same months in 2019).
While effects on overall employment are not significant at conventional levels, the point estimates
for service-providing public employment sectors in columns (3) and (4) suggest MLF counties increased
local government service employment by 422 to 517 employees relative to the control group. Interpreting
58 Baseline means vary across models because the “control group” is the intercept of the RD polynomial from the left-hand
side of the cutoff, which may vary when a control adjusts the optimal bandwidth over which the polynomial is projected.
34
estimates with respect to the control mean in column (3), this amounts to an average employment decline
of 1,200 to 1,295 employees relative to a baseline decline of 1,717 employees for ineligible counties—an
effect size of 24.6% to 30.1%, indicating a striking degree of employment smoothing in response to
emergency liquidity.59
Panels (a) and (b) in Figure 10 below, show RD scatter plots associated with our preferred estimates
of employment changes (column (4) of Table 4), both overall and for service-providing sectors.60
Figure 10: RD Plots of MLF Access Effect on Public Sector Employment
(a) ∆ Overall Employment Post-MLF (b) ∆ Services Employment Post-MLF
NOTES—Plots show regression slopes and intercepts from Equation 1 in the post-period (May and June 2020
pooled), overlaid on top of equally spaced pre-binned outcome data with a bin size of 35 (x-axis in thousands).
Plots are shown over a fixed 1 million population wide bandwidth on the running variable. Plots first residualize
employment of state-fixed effects (added back to their overall mean) prior to mean-collapsing by bin.
These plots first reveal a largely linear and negative employment-county size gradient for local public
employees—the larger the locality, the larger the year-on-year level decline in employment. Interestingly,
the same plots in the placebo period produce the opposite slope—the largest counties also had the
largest growth in public employment in the run up to the pandemic, albeit with a milder gradient (see
placebo effects in Section 6). While noisy due to the sparseness of the QCEW data, the plots reveal a
modest upward level shift in overall employment (though not statistically significant at conventional
levels in Table 4) when MLF liquidity is available, and a more pronounced statistically significant shift
for service-providing sectors, largely comprising employees at educational institutions.
59 In percentages, column (6) shows a 1.69 percentage point gain in employees on a baseline loss of 7.96%; a similar effect
size of 21.2%.
60 RD plots associated with unconditional effects from column (3) of Table 4 yield nearly identical figures.
35
5.3.1 Decomposition of MLF lending vs. CARES aid Employment Effects
To this point, we have interpreted May and June 2020 public sector employment effects at the April 27
MLF eligibility cutoffs (250,000 for cities, 500,000 for counties) as being fully attributable to the MLF
emergency lending option. However, as noted at the outset, the CARES Act announced on March 27
also provided for direct aid eligibility for cities and counties with populations over 500,000 (whereas
those under this cutoff had to rely on more uncertain state downstreaming), raising the possibility that
earlier estimates capture a combination of both direct aid and lending eligibility—though it may be
argued that both reflect similar liquidity interventions and thus likely share the same theoretical sign on
employment. To begin to disentangle the separate contributions of MLF optionality and direct CARES
Act aid, in Figure 11 we provide dynamic monthly post-period estimates corresponding to column (4)
from Table 4, leveraging the differential timing of CARES and MLF cutoff announcements.
Figure 11: Differenced RD Effects on Local Government Employment by Month
NOTES—Figure plots RD coefficients and 90% confidence intervals estimated using the specification from Table 4
column (4), with QCEW 12th of the month employment data. See Table 4 notes for further details.
Plotting RD estimates dynamically presents an important observation on April 12th—employees
recalled several weeks after the CARES Coronavirus Relief Fund (CRF) provisions were enacted, but also
several weeks before MLF population cutoffs were revised. In the data, all CRF aid was fully dispersed
(and assumed to be salient to and anticipated by budget officers) between April 15 and May 6. We thus
interpret the departure from zero that we detect on April 12th as the employment effect of anticipated
(non-downstreamed) CARES aid, whereas May and June employment effects reflect the totality of all
realized aid as well as the MLF option. The similar point estimates between April and May provide
36
initial suggestive evidence that CARES aid may have been more material in affecting hiring and recall
decisions, however the effects of the MLF expansion may also have taken some time to set in. These
dynamics also reveal an interesting pattern related to the school-year calendar, a feature we return to
when interpreting these effects. Finally, it bears mentioning that monthly estimates in placebo months
(January to March) are also reassuringly concentrated around zero prior to the onset of the pandemic in
the United States.
To more formally gauge the robustness of the result that CARES aid appears to be more consequential
than the MLF lending option for hiring, we consider a decomposition which leverages variation in
the dosage response of the MLF treatment relative to CARES aid. To see this variation clearly, in
Figure 12, we first show variation in MLF lending caps, calculated as 20% of each government’s 2017
”own-source general and utility revenue” (OSGUR) as per MLF regulations,61 and the amount of direct
aid apportioned to each government through the CARES Act based on the CRF population formula.62
Figure 12: Variation in MLF Lending Caps and direct CARES Aid Allocations
(a) MLF Lending Caps (20% of OSGUR) (b) CARES Aid CRF Allocation
NOTES—Panels use different scales. Blue filled observations in panel (a) show MLF lending caps (based on
2017 OSGUR) over the county running variable, where grey hollow observations indicate counterfactual cap
amounts that would have been implemented were there no cutoff. Blue observations in panel (b) show realized
direct aid allocations calculated from the CRF population formula (see footnote 62) plus $1, combined with data
on downstreamed aid from states to counties on the left of the cutoff. Grey observations in panel (b) denote
counterfactual aid were the population cutoff to have been perfectly binding across the entire running variable.
The two different scales of the y-axes in Figure 12 underscore that counties at the 500,000 cutoff were
61 See April 9, 2020, MLF Term Sheet for further details on MLF lending cap calculation.
62 According to the CARES Act CRF Allocation Formula, no population can be double-covered by both its underlying city
and county for aid, however each entity above the cutoff can independently claim direct aid on behalf of its constituents. We
use direct CARES aid data received by either cities or counties from USASpending.gov (the US Treasury’s official tracker of
fiscal expenditures). However, this analysis requires total county aid, which is comprised of direct county aid in addition to
direct aid paid to a county’s underlying cities. Toward this end, we split the direct city aid across counties based on the county
CRF cap were it to have accessed the aid directly. Because aid received is calculated with the “latest” population vintage, we
estimate the county-level allocation with minor error. On the left of the cutoff, we are able to complement direct aid with
indirect downstreamed aid to county governments from NACO, however do not have data on downstreamed aid to cities.
37
eligible for both an outsized amount of potential lending, and a much smaller but still material amount
of direct aid, making comparisons difficult. While the kinked nature of the CARES population formula
appears at first to provide a potential test in which a regression kink design (RKD) may help discern
between these two policies, the underlying kink is in fact a flat schedule in the variation of interest—aid
per person. That is, when both the outcome variable and treatment variable are highly correlated with
the running variable (as it is here), there is in fact no kink in the denominator since the aid allocation
formula is based on population itself, and therefore no meaningful variation in aid to leverage. Instead,
we therefore opt for an alternative dosage response interaction test that uses variation in OSGUR
\ in
panel (a) of Figure 12 (inclusive of counterfactual values, denoted with a hat), allowing us to compare
effects at the cutoff for issuers that would have been eligible for more lending, relative to similar OSGUR
\
levels below the cutoff (indicated by grey dots to the left).
Toward this end, we alter our equation of interest slightly where g now denotes geography, and t the
period of interest, and decompose the main effect into an overall level shift (β 1t ) while controlling for
the marginal effect of additional MLF lending dollars—the CARES effect when the OSGUR20
\ cap (20%
of OSGUR)
\ is set to zero—and an explicit term accounting for the marginal effect of an additional MLF
cap dollar of lending (β 2t ). Assuming the marginal MLF effect is economically meaningful relative to the
indicator value of being announced as MLF-eligible, β 1t can be interpreted as the part of the total effect
attributable to CARES aid.
Ygt = α + β 1t ∗ 1( pop ≥ cuto f f ) g + β 2t ∗ 1( pop ≥ cuto f f ) g OSGUR20
\ g + γt ∗ ( pop − cuto f f ) g (2)
+ δt ∗ 1( pop ≥ cuto f f ) g ( pop − cuto f f ) g + φt ∗ OSGUR20
\ g + Xst + ε gt
In Table 5 below, we show the results from our dosage response test, where columns (1) and (4)
use OSGUR20
\ as the main interaction term, (2) and (5) normalize OSGUR20
\ by realized CARES aid
as indicated by filled blue observations in Figure 12 (adding 1 dollar to values equal to 0 left of
the cutoff), and OSGUR20
\ normalized by counterfactual aid (CARES)
\ were it to have been allocated
formulaically across the entire running variable, including left of the cutoff. In all three of these
alternative formulations using both of our two preferred outcomes, we fail to detect a statistically
significant marginal effect of increasing the MLF cap relative to statistically significant effects on the
level shift term associated with direct CARES aid. If we were to interpret the point estimates on the
interaction term at face value, they would also only amount at most, to around 8% of the overall effect.
38
Table 5: MLF vs. CARES Dosage Response Decomposition of Employment Effects
YoY Level Changes YoY Percent Changes
(1) (2) (3) (4) (5) (6)
Constant -1473.0*** -1417.2*** -1412.3*** -10.09*** -9.967*** -9.400***
(200.3) (192.3) (180.0) (0.715) (0.665) (0.538)
1(pop ≥ cutoff) 620.3* 554.0* 531.9* 3.021** 2.959** 2.168**
(266.3) (272.2) (261.2) (0.930) (0.933) (0.810)
1(pop ≥ cutoff)*OSGUR20
\ -0.678 -0.0110
(1.408) (0.00747)
1(pop ≥ cutoff)*OSGUR20/CARES
\ 39.88 0.143
(91.57) (0.286)
1(pop ≥ cutoff)* \
OSGUR20/CARES
\ 36.71 -0.104
(140.6) (0.461)
(pop - cutoff) -3.279*** -3.164*** -3.074*** -0.00587** -0.00548* -0.00311
(0.681) (0.670) (0.644) (0.00220) (0.00215) (0.00214)
1(pop ≥ cutoff)*(pop - cutoff) -0.227 -0.218 -0.384 0.00269 0.00391 0.000710
(1.173) (1.113) (1.102) (0.00353) (0.00327) (0.00334)
OSGUR20
\ 1.135 0.0153*
(0.998) (0.00713)
OSGUR20/CARES
\ 0.594 0.0156*
(0.993) (0.00664)
OSGUR20/
\ CARES
\ 41.10 0.674*
(43.44) (0.333)
N 684 684 684 684 684 684
NOTES—Table presents estimates from Equation 2. Percents in columns (4) - (6) range from 0 to 100. Standard
errors are clustered by population relative to the cutoff (the running variable). See Table 4 notes for further details.
*** p≤0.01, ** p≤0.05, * p≤0.1.
In conjunction with prior evidence that employment effects percolated prior to the MLF cutoff
revision, and a lack of statistically significant total employment effects when analyzing the cutoff
associated with cities (250,000) which was not subject to CARES (despite evidence that effects on yields
remain at this cutoff), we take this as evidence that CARES aid induced the majority of the employment
effects, while the MLF was more relevant for financial markets.
5.3.2 Employment Effects by Credit Ratings and Calendar Month
One interesting pattern that arose in Figure 11 was that the employment response to the totality of direct
CARES aid and MLF lending eligibility was only positive in non-summer months. We further examine
this result, adding heterogeneity by January 2020 plurality ratings in Figure 13.
39
Figure 13: RD Effects on Local Government Employment by Ratings and Month
NOTES—-Figure plots RD coefficients and 90% confidence intervals estimated using the specification from Table
4 column (3) with QCEW 12th of the month employment data, separately estimated by January 2020 plurality
ratings. Here we use the specification omitting state fixed effects so not to over-absorb differences in ratings that
may differentially load on to states). See Table 4 notes for further details.
When examining effects separately by ratings, we first confirm the general pattern of only detecting
positive effects from April to June, and October to December. This school year pattern is broadly
consistent with the notion that emergency liquidity—whether aid or a lending option—supported
educational institution recalls, which is particularly striking given that the majority of schools were still
under lockdown from April to June. Interestingly, Figure 13 also reveals that these employment returns
were only sustained in the long run when the underlying government was a highly-rated issuer (which
as we showed earlier, reflects the majority of municipal bond issuers).
If indeed it is the case that the least fiscally constrained issuers were most responsive to the additional
liquidity, both during the months of April to June when government shutdowns were still widely in
place, and through the close of the 2020 calendar year, this is consistent with the hypothesis that state and
local governments may have over-weighted the worst possible outcomes based on past crisis experience,
furloughing education sector employees even though realized revenue shortfalls were far lower than
originally anticipated.63
63 This view was articulated in Sheiner (2021), which we discuss along with the evolving fiscal and jobs outlook of state and
local governments in Appendix A.1.
40
5.4 Pricing Credit Risk or Liquidity?
Above, we showed that MLF access impacted investor-perceived yields, but only at the low end of the
credit ratings distribution. This prompts the question, what exactly are investors pricing? To investigate
the mechanisms underlying these yields, we perform two additional exercises. First, in Appendix A.7.7,
we estimate the effect of MLF access on the probability an NRSRO downgrades a bond (a lagged but
very salient type of observable credit risk), and find modest evidence that MLF-eligible issuers had lower
downgrade probabilities than observationally equivalent ineligible issuers. While this is consistent with
yields predominantly pricing credit risk, in what follows we implement a more formal decomposition
test to separate yields changes arising from illiqudity versus credit risk.
5.4.1 Spreads Decomposition: Asset Price Approach
While the RD approach cleanly isolates the MLF impact from other concurrent events for the sample of
municipal bonds issued by cities and counties, in this section, we study how credit risk premia evolved
throughout the crisis to test whether unexpected increases in credit risk may have driven the larger MLF
response lower down on the credit rating distribution.
The infrequent trading of municipal bonds and a potentially large number of unexecutable quotes
make measuring liquidity and credit risk premia challenging for smaller subsets of issuers. We thus
follow the transaction-based decomposition in Schwert (2017), but decompose municipal bond spreads
at the weekly level rather than monthly. We first estimate the liquidity component of yields directly, then
interpret the predicted residual as compensation for credit default risk. For bond b issued by issuer i in
state s with yield ybist , we begin by computing the duration-matched, tax-adjusted spread for each bond,
as:
1 − τ fdeduct − τsdeduct )−1 ybist − yUST if exempt at federal-level and at state-level
bist
ŷbist =
1 − τ fdeduct )−1 ybist − yUST
bist if exempt at federal-level but taxable by state (3)
ybist − yUST
if taxable
bist
where yUST
bist is the yield-to-maturity on the bond implied by the risk-free Treasury curve at the time
of transaction minus an interpolated maturity-matched swap rate following Gürkaynak et al. (2007);
τ fdeduct and τsdeduct are the annual federal and state tax rates for a representative wealthy household
taken from the NBER-TAXSIM model, which also adjusts for local and state deductions and assumes
the marginal investor buys bonds within their resident state to take advantage of state tax exemptions.64
64 This is similar to using a state-deducted formula such as 1/ (1 − τ )(1 − τs ), which does not adjust for local deductions (see
f
41
This departs slightly from our earlier specifications as the spreads decomposition literature emphasizes
duration-matched and directly tax-adjusted yields spreads relative to safer treasury bonds.
Next, we directly estimate a weekly liquidity measure for each bond as the first principal component
λbt of a set of bond-week liquidity measures that include: (1) Amihud price impact; (2) Imputed
round-trip cost; (3) Roll measure; and (4) Price dispersion.65 Appendix A.8 provides details on the
calculation of these liquidity measures, and shows liquidity deterioration for both AAA/AA and A/BBB
city and county bonds in March 2020, although the liquidity of the lower-rated bonds declined more
deeply and took longer to recover to its pre-pandemic level (if at all, depending on the illiquidity
measure).66 To formally quantify the relative contribution of illiquidity to the rise in yields in the build
up to the crisis, we closely follow Schwert (2017) and estimate the sensitivity of spreads to liquidity βλt by
regressing the duration-matched, tax-adjusted yield on the liquidity measure, conditional on observed
ratings:
ŷbist = αt + βλt λbt + δt Ratingsbt + ε bist , (4)
where Ratingsbt contains a series of bond ratings dummy variables (AAA, AA, A, BBB, BB and below,
NR), meant to capture observable credit risk as represented by NRSRO ratings, which may be correlated
with liquidity.67 The liquidity spread component of yields (reflecting the illiquidity of a bond) is then
calculated as
lbt = βλt λbt − λ p01 (5)
where λ p01 is the first percentile of the liquidity measure’s first principal component, thus benchmarking
to a very liquid municipal bond within a given week t. The default spread—the yield compensation for
credit default risk—is then calculated as the remaining portion of the yield spread after adjusting for
Schwert (2017) for an example). We use the NBER-TAXSIM annual “Total Rate, Wages” for bonds that are exempt at both federal
and state levels (in Mergent, tax code=EXMP and state tax=N or missing), and the “Federal Rate, Wages” for bonds exempt at
the federal-level but not at the state-level (in Mergent, state tax=Y), taken from https://users.nber.org/~taxsim/state-
rates/maxrate.html (and apply 2018 tax rates, the final year of the data, to 2019 and 2020 bonds).
65 Appendix A.8 includes a specification where we calculate the liquidity factor including the effective bid-ask spread in
addition to these four liquidity measures, and the results are qualitatively unchanged. Our choice to not include the effective
bid-ask spread in the main specification is related to the sample restrictions that are required for the BAS calculation, and are
broadly discussed in the appendix.
66 A broader sample of bonds that include state bonds also exhibits a similar liquidity deterioration, which supports the
generalizability of our city and county findings to the broader municipal bond market.
67 Unlike previously, the decomposition here requires including time-varying ratings rather than fixed issuer ratings, as
time-varying ratings capture the sticky nature of credit rating revisions. Toward this end, we assign each bond the minimum
ratings among the three NRSROs, to be consistent with the MLF Term Sheet.
42
liquidity
γbist ≡ ŷbist − lˆbt (6)
which accounts for both observed credit risk (through ratings) and unobserved credit risk. This allows
us to generate the following decomposition for city and county bonds by January 2020 plurality ratings
group, plotting weekly means of default risk (γbist ) and illiquidity (lˆbt ) components, in Figure 14:
Figure 14: Illiquidity and Credit Risk Evolution in the 2020 Municipal Bond Market
(a) High-Rated (AAA & AA) City and County Bonds (b) Low-Rated (A & BBB) City and County Bonds
(c) High-Rated (AAA & AA) Week-on-Week % Change (d) Low-Rated (A & BBB) Week-on-Week % Change
NOTES—Panels (a) and (b) show the weekly average of the default and liquidity components of city and county
bond yields by rating group for each week in the 2020 calendar year (details in Appendix A.8). Panels (c) and
(d) further show week-on-week changes in both the first principal component liquidity measure (λbt − λ p01 ) and
(ŷbist ), demonstrating the relative speed in growth of overall yields and illiquidity respectively.
Panels (a) and (b) of Figure 14 demonstrate that while prior to the crisis, both observable illiquidity
43
measures and residual credit-default risk appeared to contribute meaningfully to yield spreads, the rise
in city/county yields for both high and low-rated issuers seems to have been mostly driven by the
price of default risk, with a higher contribution of credit risk to long run yields distress for low-rated
issuers—evinced by both higher underlying levels and higher contributions to adjusted yields. While
our estimates of the default component are upper bounds insofar as observed liquidity measures are
imperfect or incomplete, the large credit-default residual suggests that investor perceptions of right-tail
risk may have changed as the crisis deepened. As market functioning returned to normal, uncertainty
became more resolved and observed credit ratings may also have had more time to adjust. However,
consistent with market yields trends, credit default risk remained elevated for A and BBB bonds, while
the default risk of safer AAA and AA bonds reverted back to their mean more quickly. To understand
how greater illiquidity during the crisis did not result in a higher decomposition coefficient on liquidity
during this same period, we show in panels (c) and (d), weekly percent changes in both the liquidity
first principal component and adjusted yields. These panels clearly show that while illiquidity rose
dramatically during this period relative to pretrend (consistent with Appendix A.8), adjusted yields
grew even faster on a larger base, resulting in a somewhat stable coefficient on liquidity. The bottom line
is that the decomposition fails to attribute the large rise in yields to illiquidity, and instead assigns the
lion’s share of weight to default risk.
The large magnitude on credit risk is consistent with Schwert (2017), who found that credit-default
risk accounted for between 74% and 84% of mean spreads using a sample mostly reflecting expansion
years, suggesting that there may be a higher degree of underlying credit risk in the municipal bond
market than is commonly appreciated. Here we show that this was especially true for low-rated
issuers in the run up to peak distress during the pandemic. The high measured price of credit risk
in the municipal bond market can be due to high systematic risk, or a consequence of tax-treatment
segmentation and the inability of local retail investors at the margin to diversify idiosyncratic municipal
risk. To more precisely quantify our own estimates and compare with Schwert (2017), we report
summary statistics in Table 6 for the transaction-based bond spread decomposition. Observations are
reported at the CUSIP-week level. Yield (%) is yield to maturity. Tax-Adjusted Yield is the yield adjusted
for its tax-status and maturity in Equation 3, but not yet benchmarking to treasury yields. Tax-Adjusted
Spread (%) is the tax (maturity) adjusted yield relative to the risk-free Treasury curve (ŷbist ). Default
Spread (bps) and Liquidity Spread (bps) are the respective components γbist and lˆbt of the tax (and maturity)
adjusted spread. Default/Tax-Adj (%) and Liquidity/Tax-Adj (%) are the ratio of the Default and Liquidity
Spreads to the Tax (and maturity) Adjusted Spread.
In our preferred (unweighted) mean specification, we find that in the pre-crisis period, default risk
44
accounted for about 73.2% and 79.4% of yields for high- and low-rated bonds respectively. During the
crisis, these rose to 89.1% and 88.5% respectively, and remained elevated post-intervention, especially
among low-rated bonds (86.3% versus 82.4%). We interpret the persistently higher default risk share
among lower rated bonds as a potential explanatory factor in the slower recovery of lower rated bonds
in the overall market, and as suggestive evidence for why MLF seems to have an outsized impact on
lower rated bonds (whose credit risk was particularly elevated during this period).
45
Table 6: Spreads Decomposition Summary Statistics, City and County Issuers
Pre Outbreak/Peak Interventions/Post
Mean Weighted Mean SD # Observations Mean Weighted Mean SD # Observations Mean Weighted Mean SD # Observations
(1) (2) (3) (4) (5) (6) (7) (8) (9) (10) (11) (12)
A. Liquidity Measures
BAS 0.62 0.54 0.58 353 0.72 0.61 0.67 650 0.67 0.55 0.68 4,182
IRC (%) 0.57 0.51 0.55 6,711 0.63 0.56 0.62 5,394 0.63 0.57 0.61 47,528
Roll 0.86 0.85 0.94 6,711 1.30 1.15 1.33 5,394 1.08 1.07 1.13 47,528
Dispersion 0.28 0.26 0.27 6,711 0.35 0.36 0.33 5,394 0.33 0.32 0.30 47,528
Amihud (% per $1m) 23.1 9.87 35.3 6,711 22.7 11.2 34.5 5,394 23.7 12.6 34.8 47,528
First PC 1.26 1.05 1.24 6,711 1.55 1.35 1.36 5,394 1.46 1.28 1.33 47,528
B. AAA/AA Sample
Yield (%) 1.72 1.78 0.90 5,511 2.29 2.51 1.10 4,728 1.70 1.86 1.07 38,937
Tax-Adjusted Yield (%) 2.87 2.85 1.09 5,511 3.96 4.25 1.82 4,728 2.92 3.07 1.67 38,937
Maturity-Adjusted Spread (bps) 11.1 10.4 10.0 5,511 28.3 30.1 17.9 4,728 21.0 21.3 15.7 38,937
Liquidity Spread (bps) 2.97 2.45 3.00 5,511 3.07 2.58 2.63 4,728 3.68 3.13 3.42 38,937
46 Default Spread (bps) 8.12 7.97 9.40 5,511 25.2 27.6 17.8 4,728 17.3 18.2 15.4 38,937
Liquidity/Mat-Adj. (%) 26.8 23.5 10.9 8.55 17.6 14.7
Default/Mat-Adj. (%) 73.2 76.5 89.1 91.5 82.4 85.3
C. A/BBB Sample
Yield (%) 2.36 2.98 1.22 922 2.79 3.22 2.16 487 2.69 3.57 1.41 6,980
Tax-Adjusted Yield (%) 3.44 3.74 1.48 922 4.32 5.18 2.65 487 4.30 5.62 2.09 6,980
Maturity-Adjusted Spread (bps) 16.3 19.1 14.2 922 31.8 38.1 26.2 487 34.6 46.7 20.3 6,980
Liquidity Spread (bps) 3.35 3.05 3.14 922 3.67 2.20 3.32 487 4.75 4.34 4.05 6,980
Default Spread (bps) 12.9 16.0 13.9 922 28.2 35.9 25.9 487 29.8 42.4 20.1 6,980
Liquidity/Mat-Adj. (%) 20.6 16.0 11.5 5.78 13.7 9.28
Default/Mat-Adj. (%) 79.4 84.0 88.5 94.2 86.3 90.7
NOTES—Here, we show decomposition summary statistics for three representative periods: Pre-Crisis (January 6 - March 1), Outbreak/Peak (March 2 - March
22), and Post-Intervention (March 23 - Dec 31). Weighted and unweighted means refer to whether measures in the regression are weighted by par volume
traded (see Appendix A.8 for further details).
6 Robustness and Sensitivity
6.1 Placebo RD Plots Prior to Crisis
Below we show RD estimate plots associated with prior regression output shown in the main body of
the text, using our preferred specification that includes state and month fixed effects to absorb volatility
given the small sample size involved in cutting results by credit ratings bin. Figure 15 shows yield
RD plots for the placebo period by creditworthiness, while Figure 16 shows employment RD plots
for the placebo period using our two difference in discontinuity strategies. These plots show relative
smoothness across the cutoff, consistent with the tables showing no statistically significant RD effect
prior to the policies being implemented.
Figure 15: RD Placebo Plots of MLF Access Effect on Yields by Credit Worthiness
NOTES—Plots show regression slopes and intercepts from Equation 1 in the pre-period, overlaid on top of equally
spaced pre-binned outcome data with a bin size of 20 (x-axis in thousands). Plots are shown over the optimal
bandwidth selected using the IMSE-procedure, which produces (potentially) asymmetric optimal bandwidth
boundaries for each sample. Plots correspond to Table 2, which includes state and calendar month fixed effects
as controls. Plot thus residualizes all yields by state-fixed effects (added back to their overall mean) prior to
mean-collapsing by bin.
47
Figure 16: RD Placebo Plots of MLF Access Effect on Public Sector Employment
(a) ∆ Overall Employment, Pre-MLF (Placebo) (b) ∆ Services Employment, Pre-MLF (Placebo)
NOTES—Panels (a) and (b) show year-on-year differences in public employment for the months of January and
February, 2020, relative to January and February, 2019. Results are shown for the differenced RD strategy discussed
in the text, pooling all issuers in one sample. This RD does not yet implement an IMSE-optimal bandwidth. The
baseline number of local employees in a given locality in 2019 was about 750 employees. Source: QCEW, May 26,
2021, Q4 release (through December)
6.2 Manipulation Tests
Below we show formal McCrary (2008) running variable manipulation tests, using the Cattaneo et al.
(2018) method of local polynomial density estimation with robust standard errors, where bandwidths
for density tests are data-driven and thus do not have to span the whole support of the histogram.
Figure 17: Manipulation Test for City and County Population Running Variables
(a) Density Test for City Populations: (b) Density Test for County Populations:
NOTES—Figure separately plots histograms of unique cities and counties on either side of their respective MLF
population cutoffs, and estimates 95% confidence intervals from local polynomial fits on each side of cutoff
using the Cattaneo et al. (2018) method. Significant overlap in confidence intervals signifies a passing test. City
manipulation density test is overlaid on top of a histogram with binwidths of 10,000 while county manipulation
density test is overlaid on top of histograms with binwidths of 25,000 (due to there being fewer counties than
cities). Fractions are small because majority of cities and counties fall below 100,000 and 200,000 in population
respectively.
48
Consistent with cutoffs being chosen using round-number heuristics and the MLF’s regulatory
population eligibility being lagged by 1 to 2 years, we find no evidence of cutoff manipulation by
policymakers, nor cutoff-targeting based on the underlying distribution of of issuers. We also provide
p-values from a density manipulation test associated with a discrete running variable (Frandsen (2017)),
should lumpy population observations be interpreted as discrete rather than continuous. The Frandsen
(2017) test of equality of projected intercepts at the cutoff produces to a p-value of 0.967 for counties, and
0.388 for cities, significantly away from conventional p-values that would reject equality.
49
6.3 Sensitivity to Controls
Here we report sensitivity of our main RD yields estimates to controls and sample restrictions, where column (6) is our preferred specification.
Table 7: RD Effects on Yields, Sensitivity to Controls and Restrictions
(1) (2) (3) (4) (5) (6) (7) (8) (9) (10) (11) (12) (13)
a. Pooled Post:
Current Yield (Overall) -17.66 -10.02 -11.29 -11.42 -18.75 -16.36 -19.42 -20.68 -19.69 -20.13 -20.62 -21.26 -20.39
City Only -22.00 -13.11 -13.56 -13.60 -25.38 -24.41 -27.92 -30.52 -28.08 -27.07 -26.67 -25.73 -23.26
County Only -16.85 -20.90 -23.04 -23.00 -13.64 -12.04 -16.04 -13.68 -16.59 -14.67 -14.40 -16.27 -21.06
High-Rated (AAA & AA) 8.67 4.14 4.20 4.29 -1.30 0.22 -1.74 -3.17 -1.94 -1.57 -2.16 -7.93 -6.99
Low-Rated (A & BBB) -132.40** -123.17*** -122.60*** -122.39*** -73.20** -73.09** -75.43** -77.05** -75.99** -65.61* -67.62** -60.27* -56.14*
b. Pooled Pre (Placebo):
Current Yield (Overall) -9.41 -6.12 -6.78 -6.93 -14.62 -13.01 -13.26 -13.52 -14.66 -13.51 -13.62 -11.71 -11.26
City Only -1.01 -1.18 -1.31 -1.26 -8.30 -8.11 -9.34 -9.52 -11.13 -8.26 -8.09 -5.47 -5.10
County Only -42.47 -24.49 -26.48 -26.81 -24.05 -22.29 -21.61 -19.84 -19.46 -20.23 -20.42 -22.40 -24.29
High-Rated (AAA & AA) 1.21 1.54 1.67 1.93 -5.90 -4.96 -6.09 -6.60 -5.67 -5.68 -5.86 -7.13 -5.73
Low-Rated (A & BBB) -77.80** -57.08** -55.54** -55.58** -22.19 -23.53 -25.14 -25.95 -31.68 -16.35 -19.06 -21.98 -20.79
Fed. Tax Adjust X X X
St. & Fed. Tax Adjust X X
50 State FE X X X X X X X X X
Month FE X X X X X X X
Revenue/GO Bond X
Day/Week of Trade X
Maturity Size X
Amount Outstanding X
Tenor Length X
Remaining Duration X
Sample Restrictions X X X X X X X X X X X X
NOTES—Sample restrictions include 1% winsorizing and outlier filtering. See Table 2 notes and text for further details. *** p≤0.01, ** p≤0.05, * p≤0.1.
Column (2) applies the NBER-TAXSIM deduction-adjusted top federal tax rate for a wealthy household to all exempt bonds, and assumes the
marginal investor buys bonds outside of their resident state. Since local coupon payments are exempt from state tax liabilities, it is optimal in
most states for individual investors to invest in within-state issuers. Columns (3) and (4) therefore apply both federal and state effective tax
rates to double-exempt bonds, and federal rates to federal-exempt only bonds, assuming the marginal investor resides in the state. That is, for
this specification, we apply 1/(1 − τ fdeduct − τsdeduct ) to tax-exempt yields, which accounts for both local and state tax deductions.68
68 This is similar to using a state-deducted formula such as 1/ (1 − τ )(1 − τs ), which does not adjust for local deductions. See, for example, Schwert (2017).
f
From columns (4) onward, we include state fixed effects that absorb 2020 state-tax adjustments (the
coefficient difference between (4) and (5) is thus coming entirely from Federal-exempt only bonds that
are eventually absorbed by month fixed effects). While perfect balance among the low-rated A and BBB
group requires conditioning on these state fixed effects (to partial out volatility from the smaller sample),
we interpret this as forcing crisper comparisons due to divergence in early 2020 (when low-rated issuer
states were less balanced and trading volume low). These concerns however, should be minimal
given that unconditional raw mean trajectories in the symmetric 100,000 population bandwidth (Figure
6) demonstrated that pretrends were relatively parallel (especially in the run up to the first Federal
announcement). All other ratings groups are otherwise unconditionally balanced, as indicated by the
lack of point estimate statistical significance in the placebo period.
6.4 Yields Sensitivity to CARES Act Notch in CRF Aid Formula
While the above manipulation test confirms that cutoffs were not chosen based on the underlying
variation in issuers, it does not rule out the possibility that these heuristic population cutoffs could be
binding for other government policies, confounding our interpretation of the intervention. As discussed
in the context of employment effects, we identify one potential confounding policy: the March 27th
CARES act included a Coronavirus Relief Fund (CRF) provision that “local governments serving a
population of at least 500,000, as measured in the most recent census data, may elect to receive assistance
directly from Treasury. Such direct local assistance allocations reduce the allocation that is made to the
state government (keeping the state allocation constant).”69 In other words, localities over 500,000 in
population may have had quicker or more direct access to CRF aid, relative to localities just under that
cutoff that had to rely on downstreaming from their underlying state allocation cap.70 Since allocation
caps were fixed to the right of this cutoff, but unrestricted to the left, the amounts received may have
been differentially higher or lower to the right of the cutoff.
As discussed, this poses a potential problem for counties in our analysis, which are subject to
the April 27 MLF population cutoff (also using 500,000 as an eligibility threshold). In the context
of yields, we are served by two additional tests to help us tease apart CARES from MLF effects,
which were not available in our employment analysis. We first note that visually, we have substantial
variation in the month that elapsed between the CARES and MLF revision announcement. During this
inter-announcement interval, yields appeared to trend almost identically (shown in Figure 6), whereas
they separated earlier among employment outcomes. Second, only one of the two cutoffs (counties)
69 https://crsreports.congress.gov/product/pdf/R/R46298.
70 CRF aid allocation caps for localities greater than 500,000 in population are calculated as the product of the total state
allocation (based on population) weighted by locality population share.
51
were aligned exactly at 500,000, whereas the other cutoff (cities) was not. We thus show in Figure 18
the variation underlying our main results for low-rated (A & BBB) yields, excluding counties from the
analysis and thus only focusing on the 250,000 city population cutoff which is unimpaired by CARES
aid—or at least, only affected far away from the cutoff in a way in which the RD polynomial can fully
control for.
Figure 18: Mean Yields within 100k of MLF Population Cutoff, Low-Rated (A & BBB) Cities Only
NOTES—Figure shows mean weekly yields (pooled over buyer and seller prices) for low-rated city eligible
issuers with cutoff-relative populations between 0 and 100,000 inclusively (blue dashed series), and issuers with
cutoff-relative populations greater than or equal to -100,000 and less than 0 (red solid series). Trades between
announcements are pooled into a single period beginning on the announcement day. See text for sample
restrictions and definitions. Source: MSRB, S&P, Moody’s, Fitch
This additional placebo test shows a very similar pattern to our main results including counties, and
our yield RD estimates for low-rated cities are similarly robust and statistically significant. While the
results for employment are less conclusive, we can more confidently claim that investors seem not to
have responded to CARES act aid, whereas they did respond to an MLF emergency liquidity option.
7 Discussion and Remaining Puzzles
We estimate the option value of municipal liquidity by studying bond market activity and public sector
hiring decisions when government budgets are severely distressed. The option is made available due
to a number of Federal sector facilities that were announced after the onset of the COVID-19 pandemic,
which simultaneously shocked incomes and resulted in a liquidity crisis in the municipal bond market.
We first show that overall secondary market yields and primary issuance for the most part returned
to normal market functioning as a result of the totality of Federal interventions that were introduced
between mid-March and the end of April 2020, while low-rated investment grade bonds remained
52
relatively distressed. To estimate the option value, we use a regression discontinuity (RD) design that
exploits lending eligibility cutoffs introduced by the Federal sector’s Municipal Liquidity Facility (MLF)
on April 27, 2020. This granted direct Federal Reserve lending eligibility via a Special Purpose Vehicle
to city issuers with populations greater than 250,000, and county issuers with populations greater than
500,000. We first estimate the value of this differential access to emergency liquidity using municipal
bond yields as an investor perceived measure of access. We find that low-rated (A and BBB) government
issuers’ bonds traded at higher prices with facility access. Low-rated issuers that were narrowly eligible
for emergency lending immediately exhibited a yields decline of roughly 75 basis points relative to
issuers that narrowly missed eligibility—a magnitude that closely corresponds to the overall municipal
market spread between BBB yields and higher-rated issuers. We find modest evidence that eligible
issuers experienced lower credit downgrade probabilities overall, and stronger evidence that MLF
optionality translated to differential primary issuance on private markets. Using a complementary asset
price decomposition approach, we quantify the credit-risk channel over a broader set of issuers, which
implies a non-trivial role for credit risk in determining yield spreads during crises.
We then show that local governments, in contrast to investors, responded to the totality of MLF
optionality and direct CARES aid by retaining 25% to 30% more service-providing public sector
employees (reflecting educational institutions) in light of mass furloughs and separations that were
prevalent during this period. These employment smoothing improvements are detected predominantly
among high-rated issuers (the majority of governments) and were strong even when schools remained
shut down, consistent with a viewpoint that state and local governments may have over-weighted the
worst possible outcomes (based on past experience) in furloughing education sector employees given
realized revenue shortfalls were far lower than originally anticipated (Sheiner (2021)). The timing of the
effects and ancillary decomposition tests suggest that most of the return in employment is attributable
to direct CARES aid rather than MLF lending (consistent with CARES employment effects estimated
in Green and Loualiche (2020)). When the additional liquidity through both interventions became
available as potential buffer for the locality’s revenue position, this may have counteracted some of the
uncertainty that induced the initial furloughs. Taken together, our results imply municipal debt market
and employment outcomes would likely have been more distressed absent the MLF facility’s operation
and CARES aid respectively.
Interestingly, these results also suggest the presence of a potential credit-risk sharing channel on
top of the Fed’s role as lender of last resort. This brings up a number of questions and puzzles that
future research will need to address. Is emergency liquidity only valuable at the low end of the ratings
distribution because in response to adverse shocks, extra liquidity provides implicit insurance against
53
credit risk? If so valuable, why did only two issuers take up direct facility lending?71 We provide two
candidate explanations here: the first relates to the combination of the MLF’s restricted eligibility and
the design of the penalty pricing grid (shown in Appendix A.2). While part of the facility’s rationale was
that issuers simply could not find markets to match their target issuance due to a general liquidity freeze,
a more nuanced view is that eligible issuers could in fact find matches, especially after the market began
to normalize, but only used the MLF when its prices were more favorable than those offered through
a competitive bidding process. It would, for example, be in an eligible issuer’s interest to access the
MLF if the issuer’s rating was substantially higher than the bond being issued, as the facility penalty
prices are at the issuer rather than issuance level. Indeed, on some occasions eligible issuers appear to
have conducted just such a comparison. In one of those cases, the state of New Jersey decided to issue
publicly after considering MLF rates,72 while in another, MTA chose MLF.73 A second explanation relates
to stigma in borrowing, which may have deterred issuers as suggested by Armantier et al. (2015) and
Moore (2017) who studied the Fed’s Discount Window and Term Auction Facility, respectively.
A second question is if the facility provided short-term assistance to new primary issuance, how did
this support pass through to long-term secondary market yields? We begin the discussion by noting that
sufficient liquidity is necessary for municipalities to meet spending obligations like payroll, debt service,
and other fixed payments, as well as unforeseen circumstances.74 Municipality access to short-term
borrowing can allow such payments, including those related to long term debt, to be made.75 Fiscal rules
or bond covenants may prohibit the proceeds of new debt issuance to be used for debt repayment, but
because cash is fungible, access to liquidity can be used to fund non-debt expenses, like payroll, thereby
freeing up resources to be used for debt service. Finally, by avoiding unnecessary public employee
layoffs or tax increases, short-term financing may help to preserve the local tax base from which the funds
for long term bond repayment are drawn. Each, or all, of these mechanisms is a potential connection
between the kind of short-term assistance offered by MLF and the performance of long-term debt.76
Given our new estimate of the willingness to credit-risk share, a parameter which enters a
broader welfare calculus regarding the efficiency of macroeconomic stabilization policies, and sizable
71 Illinois has issued via the MLF twice, for a total $3.2 billion in loans (of its $9.67b MLF state borrowing cap), while the
New York Metropolitan Transit Authority (MTA) has also issued twice, totaling roughly $3.35 billion, equal to its cap.
72 https://www.reuters.com/article/usa-new-jersey-fed-bonds/new-jersey-picks-muni-market-over-fed-for-
4-billion-bond-sale-idUSL1N2HD1ZD.
73 https://www.spglobal.com/marketintelligence/en/news-insights/latest-news-headlines/new-york-s-mta-
sells-over-450m-in-debt-to-fed-s-municipal-liquidity-facility-59983543.
74 Indeed, cash on hand is a major factor in determining bond ratings. See Moody’s July 2020, pages 9-12 (Moody’s Investors
Service, 2020).
75 In addition to making payments directly to bondholders, municipalities may be required by bond covenants to maintain
a liquid sinking fund sufficient to cover several months of debt service.
76 In ongoing work, we are also exploring whether we can leverage differences in fiscal rules and features of outstanding
long term bonds (such as revenue versus GO), to try to address this apparent short term to long term mechanism.
54
employment effects, one natural question is when does municipal credit-risk sharing represent a socially
efficient policy improvement? From a financial frictions viewpoint, several influential papers have
suggested that sub-optimal risk sharing could arise if institutional investors are overly concentrated
in locally exempt bonds—a home market bias that distorts the efficient spread of risk (Poterba (1989),
Pirinsky and Wang (2011), Schwert (2017), Babina et al. (2021)). Other market structure constraints
may also result in inefficient muni market pricing (Garrett (2020)). If financial frictions pass through
to labor market frictions or revenue sources that have positive fiscal multipliers or high public service
externalities (high social value), these too, enter the welfare calculus. When such frictions are also
heterogeneously correlated with the mean income of underlying geographies, inequality weights must
also be taken into consideration. Due to these complexities and the many models that could rationalize
such trade-offs, we leave to future work analysis of the social efficiency of such a policy with so many
diverse potential mechanisms, as well as questions related to what issuance would have looked like were
the penalty pricing schedule steeper down the ratings distribution, or less punitive overall.
55
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A Appendices
A.1 Forecast Evolution of State and Local Government Revenue and Employment
As the pandemic took hold in the US during spring and summer of 2020, many analysts predicted
extremely dire consequences for the revenues of state and local governments. In addition to expected
delays in the receipt of final settlements of 2019 personal income tax liabilities associated with the delay
of the federal filing deadline (described in more detail in the text), disruptions to economic activity
threatened virtually all forms of the sector’s revenues.
One analysis (Fiedler and Powell (2020)), using data from previous downturns, suggested that each
year over year percentage point increase in the unemployment rate had historically been associated
with a $45 billion deterioration in the fiscal situation of state and local governments, the vast majority
of which consists of revenue declines associated with reduced economic activity. In April 2020, the
unemployment rate stood at 14.7%, a stunning 11.1 percentage points higher than its year-earlier level
(and 11.2 percentage points above its level of two months earlier, in February 2020). This suggested
an annual fiscal shock of around $500 billion to the sector. Fiedler and Powell (2020) describe several
sources of uncertainty in this estimate, including reasons to expect the shock to be larger (for example,
business closures may mean that the sales tax elasticity to unemployment may turn out to be larger than
usual) or smaller (the increase in unemployment was unusually concentrated among low wage workers,
reducing the income tax elasticity to below normal levels).
By mid-summer, it was becoming clear that at least some of the sharp increase in the unemployment
was transitory. By July, the rate stood at 10.2%, still far above its year-ago level, but already down
450 basis points from its April peak. Estimates from this period suggested state fiscal impacts in the
neighborhood of $75-100 billion for fiscal 2020, and $100-300 for 2022 (Dadayan (2020) and McNichol
and Leachman (2020)); Auerbach et al. (2020) estimated a FY 2021 effect of $167 billion for state and local
governments combined).
By mid-autumn, unemployment was down to 6.7%, and it had become clear that the most dire
concerns for the sector were off the table. In addition to the sharp rebound in unemployment, federal
fiscal support in the form of enhanced unemployment benefits, frequently taxable at the state level, had
passed through to state income tax revenues, and indirectly to sales taxes. Consumption was still below
its pre-Covid levels, but had fallen far more sharply for services rather than more heavily-taxed goods.
These subtle variations in the changes in tax bases generated significant heterogeneity in the revenue
experience of states. One bright spot in the outlook was property taxes, which held firm for the first
three quarters of calendar year 2020, and given high house price growth seemed likely to remain strong
into 2021. Nonetheless, the sector as a whole had shed over 1.3 million jobs by November, primarily in
local education, and concerns for state and local governments remained heightened.
By early 2021, as it became more clear that realized revenue losses were lower than anticipated, some
analysts began to note that government employment had declined at a far steeper rate than revenue,
and that budget cuts were both faster and deeper in scale than during the Great Recession, which was
far more gradual. (Bloomberg, Jan 2021). For example, Sheiner (2021) attributed this to preemptive and
perhaps over-cautious cuts in the education sector due to high uncertainty: “...there is also evidence that
tight fiscal conditions have led to employment declines in local education, which accounts for roughly
5% of the overall U.S. workforce. Furthermore, state and local governments, having been scarred by the
Great Recession, are likely being very cautious about spending given the tremendous uncertainty about
the economic outlook...”. Both the long-term stress from the Great Recession, and the sharp pattern
following the COVID pandemic, can be seen clearly in Figure A.1.
A.1
Figure A.1: State & Local Government Employment over the Great Recession and COVID Pandemic
NOTES—Calculations from Current Employment Statistics (CES) acquired from FRED, Economic Research
Division, Federal Reserve Bank of St. Louis. Series: CES9092000001+CES9093000001, Thous. of Persons+Thous.
of Persons, Monthly, Seasonally Adjusted. Data through May, 2021.
A.2
A.2 MLF Pricing Grid
Figure A.2: MLF Pricing Grid
NOTES—Figure shows penalty pricing grid by issuer ratings when it was announced on May 11, 2020, and revised
on August 11, 2020, for different loan term lengths. OIS = overnight index swap rate, meant to represent prevailing
private market interest rates, here pulled on May 27, 2020, and August 12, 2020, respectively. Dotted line indicates
distinction between “high” and ”low” rated issuers as defined in the draft. Pricing schedules are similar with
slight variations for different tenors. See MLF Pricing Term Sheet for further details.
A.3 Matching MSRB Issuer Names to Census Populations
Our goal is to assign a single Census population to any city, county, or state municipal bond issuer
that has traded on the secondary market at any point since Jan. 1, 2019, including all MLF eligible and
ineligible issuers. We start with the term-sheet referenced U.S. Census Bureau datasets that include
2018 city populations greater than 50,000, and 2019 county populations greater than 50,000.77 This
provides populations for larger issuers, however we also desire to match populations to smaller issuers
so that they may contribute to the RD running variable further away from the cutoff. Toward this end,
we complement our analysis with the full population Census file “sub-est2019 all.csv”, a place-level
77 U.S. Census Bureau, “Annual Estimates of the Resident Population: April 1, 2010 to July 1, 2018” for cities, as of April 6,
2020; and U.S. Census Bureau, “Population, Population Change, and Estimated Components of Population Change: April 1,
2010 to July 1, 2019” for counties, as of April 6, 2020.
A.3
dataset with both 2019 and 2018 populations for localities of all populations.78 This file contains a place
description such as the city or county’s name (which is always followed by the type suffix, such as
”CITY” or ”COUNTY”), state, census place code, and geographic code level (sumlev), allowing us to
isolate the administrative name and its geographic level.
We desire the dataset be uniquely identified by city (county) name and city (county) state, so reshape
wide the 2018 (2019) populations by sumlev, which produces a maximum of 6 potential population
measures for each geographic code, corresponding to the number of unique values sumlev can take:
1. Minor Civil Divisions (MCDs)79
2. MCD “parts”
3. County place parts
4. Incorporated places (cities, towns, boroughs, villages)
5. Consolidated cities
6. Consolidated city parts
The data separately document localities whose “part” or “balance” spills over into another locality,
which we subsequently drop (i.e. we drop (2) and (6)).80 We then designate a rule to choose among these
candidate populations. Most places have one or two population measures, but they will not have all six.
If all non-missing populations are the same, or if there is only one population, we use that population.
If any of the populations are different (0.1% of localities (27 observations; 3 of which ultimately do not
merge to MSRB-Bloomberg)), we flag and omit them the analysis.
Finally, we go through a multi-step process to merge MSRB issuer names (from their security
descriptions) to Census place names. This involves flagging duplicate MSRB place names within state
which arise erroneously from our cleaning algorithm, and remapping them based on their original
security description to their appropriate population. For example, ”SPRINGFIELD TOWNSHIP, NJ” in
the Census may correspond to ”SPRINGFIELD, NJ” in MSRB trade data; by removing the township
suffix, we can match these. But doing this universally risks false positives in other cases: for
example, the Census might contain ”HEMPSTEAD VILLAGE, NY”, ”HEMPSTEAD TOWN, NY”, and
”HEMPSTEAD CITY, NY” (all separate localities), while MSRB may only contain one HEMPSTEAD,
NY. Removing suffixes here would lead to duplicate matches. We thus only remove such suffixes when
the resulting merge is one-to-one, causing a loss rate of 4% of unmatched trades.
We also consider special treatment for matching fully consolidated cities (e.g. City and County of San
Francisco) which have only one set of issuers at either the city or county level, and partially consolidated
city-counties (e.g. Miami City vs. Dade County) which may have different revenue sources. We follow
the MLF term sheet in assigning these cases to city and/or county eligibility lists based on the revenue
sources of underlying issuers. Lastly, we manually flag potential counties that issue on behalf of cities
(“downstreamers”) based on their detailed issuer and security description. Among issuers with a reliable
MSRB issuer name and actively trading post-2019, our final cleaning procedure results in 6,143 city (1,880
county) BaseCUSIPs (unique at the issuer level) that match a population to MSRB data, and 361 city (41
county) issuers that do not retrieve a match.
78 The sub-est2019 all.csv file can be found here: https://www2.census.gov/programs-surveys/popest/datasets/2010-
2019/cities/totals/.
79 States in New England, New York, and Wisconsin, all classify towns as MCDs.
80 A “balance” is a consolidated city minus the semi-independent incorporated places located within the consolidated city
(overlapping service populations which would be double counted if we did not drop them). Incorporated places can cross
both county and Minor Civil Division (MCD) boundaries. In such cases a separate record indicates the population estimates
for the part of a place in each of its parent counties or MCDs. For such records, the place name is sometimes followed by the
designation ”pt” (which stands for part), allowing us to isolate these cases.
A.4
A.4 Data Cleaning
A.4.1 MSRB
Since January 1998, MSRB has required registered dealers to report all municipal bond transactions. The
trade record includes information about CUSIP, date and time of the trade, price and yield, maturity,
coupon, and a flag whether the dealer bought from a customer, sold to a customer, or whether it is an
interdealer trade. In January 2015, MSRB started to publicly disseminate those transactions with up to a
15 minutes delay.
We first keep unique observations at the CUSIP—trade date—RTRS Control Number level, using
the RTRS PUBLISH DATE and RTRS PUBLISH TIME variables to ensure that duplicates are not arising
from missing data. Then, in addition to the sampling restrictions applied to our RD analysis, for the
yield decomposition sample, we further apply the following conditions:
1. Delete CUSIPs with:
(a) missing coupon and maturity information for all trades
(b) a listed coupon greater than 20%
(c) a listed maturity over 100 years
(d) fewer than 10 trades in the entire sample
2. Delete transactions where:
(a) the price is less than 50 (i.e., 50% of face value)
(b) the price is greater than 150 with a short time to maturity
(c) trade date is after the maturity date of the bond
A.4.2 Mergent
The key characteristics from Mergent that we use include CUSIP, issuer name, offering amount, source
of funds and use of proceeds, bond credit rating as rated by S&P, Moody’s, and/or Fitch, coupon type
(fixed, variable, or zero), the tax status of the coupon payments, callability and first call date, insurance
status and the identity of the insurer, and pre-refunding status and timing. The Mergent data ratings
provide a longer time series of ratings data relative to the Bloomberg ratings data used in the RD analysis.
A few of the variables require some adjustments. Specifically:
Coupon Type: Mergent’s variable coupon code indicates the coupon type. However, for fixed-rate bonds
issued at a discount or at a premium, it only indicates OID and OIP respectively. Most of these bonds are
fixed-rate, nevertheless for these bonds we also use the VARRATE table to determine the coupon type.
Ratings: There are also duplicate observations at the CUSIP—rating type—rating date level, sometimes
with different ratings values. Rating agencies submit revisions of ratings that are then posted in the
Mergent database as a new rating instead of a revision to a current rating. The data provider is in the
process of correcting that in its database, so for such observations we use ratings data from Bloomberg.
A.5 NRSRO Ratings Concordance and Plurality Ratings
Each of S&P, Moody’s, and Fitch, maintain separate ratings systems for long and short-term bonds. S&P
and Moody’s also use separate systems for short-term municipal note ratings. We map of each these to
8 aggregate ratings bins that are guided by S&P’s convention: AAA, AA, A, BBB, BB, B, C, D. To do so,
we use the following concordances, which were developed manually in consultation with a number of
sources.81 The resulting columns ending in agg form the basis of our plurality ratings, calculated as the
81 These include S&P reference, Moody’s reference, and Fitch reference. Some disaggregated ratings are identified from
MSRB trades rather than the NRSRO’s themselves, however have natural mappings.
A.5
plurality across long-term, short-term, and muni-note bonds based on their “aggregate” ratings.
Figure A.3: Ratings Concordances to Aggregated Credit Rating Bins
A.6
A.6 List of A and BBB Issuers within 100k of Cutoff
Table A.1: Low-Rated (A and BBB) Issuers within 100k of MLF Cutoff
BaseCUSIP Issuer Name State Issuer Type Number of Cusips Above100
650367 Newark NJ Local Government 89 1
119677 Buffalo NY Local Government 81 1
889278 Toledo OH Local Government 73 1
86607C Summit County OH County Government 58 1
46360R Irvine CA Local Government 37 1
46360T Irvine CA Local Government 35 1
660393 North Las Vegas NV Local Government 34 0
825434 Shreveport LA Local Government 31 0
549310 Lucas County OH County Government 29 0
463805 Irving TX Local Government 28 0
759861 Reno NV Local Government 27 1
79307T St Paul MN Local Government 25 1
70643U Pembroke Pines FL Local Government 24 0
10047 Akron OH Local Government 22 0
85233S St Louis MO Local Government 22 1
555542 Macon Bibb County GA Local Government 21 0
270764 East Baton Rouge Parish LA County Government 20 0
79488C Salinas CA Local Government 19 0
759829 Reno NV Local Government 16 1
743787 Providence RI Local Government 15 0
133402 Cameron County TX County Government 14 0
86607D Summit County OH County Government 13 1
537374 Little Rock AR Local Government 10 0
534310 Lincoln NE Local Government 9 1
43615F Hollywood FL Local Government 9 0
613549 Montgomery County OH County Government 8 1
650366 Newark NJ Local Government 8 1
55553N Macon Bibb County GA Local Government 8 0
690278 Overland Park KS Local Government 7 0
66041H North Las Vegas NV Local Government 7 0
79164T St Louis MO Local Government 6 1
743940 Providence RI Local Government 5 0
702521 Pasco County FL County Government 4 1
29634D Escondido CA Local Government 4 0
344610 Fontana CA Local Government 2 0
607715 Modesto CA Local Government 2 0
928844 Volusia County FL County Government 2 1
873477 Tacoma WA Local Government 2 0
696712 Palmdale CA Local Government 1 0
759830 Reno NV Local Government 1 1
51672 Aurora IL Local Government 1 0
768861 Riverside CA Local Government 1 1
35895 Anne Arundel County MD County Government 1 1
NOTES—Data contain 43 unique issuers with 831 unique outstanding bonds or notes. Each bond contributes
additional variation to RD estimates, however inference only leverages differences between issuers (standard
errors clustered by relative population). 20 issuers are above the MLF cutoff, while 23 are below. Irvine, Newark,
North Las Vegas, Reno, and St. Louis are listed twice, but these reflect different issuers within those cities (for
example, economic development corporations may issue their own independent debt).
A.7
A.7 Additional Results
A.7.1 Yields Trends Disaggregated by Rating
In Figure A.4 below, we show more detailed variation behind our aggregated low-rated yields results
(from Figure 6 of the main draft), disaggregated by A and BBB issuers separately.
Figure A.4: Mean Yields within 100k Population of MLF Cutoffs, Separately for A and BBB
(a) A-Rated Issuers in Jan 2020: (b) BBB-Rated Issuers in Jan 2020:
NOTES—Figure shows mean yields for two subgroups: eligible issuers with cutoff-relative populations between
0 and 100,000 inclusively (blue dashed series), and issuers with cutoff-relative populations greater than or equal
to -100,000 and less than 0 (red solid series). See text for sample restrictions and subgroup definitions.
A.7.2 Dynamic Yields RD Estimates
In Figure A.5, we report coefficients from looping through our main RD specification for low-rated
issuers, estimated bi-weekly across the support of our sample frame. The specification is identical to
Table 2, but omits calendar month fixed effects which are absorbed by the sampling restriction of keeping
each 2-week period respectively, and extends the sample period reflecting the latest data.
Figure A.5: Dynamic RD Estimates of MLF Access on Secondary Market Yields
NOTES—Estimates and 90% confidence intervals shown looping over bi-weekly intervals of the support, and
collapsing all observations between announcement dates into one estimate (consistent with main results). See
sample restrictions and notes associated with Table 2 for further details.
A.8
A.7.3 Kernel Weights and Sensitivity to Bandwidth and Kernel Choices
In Figure A.6, we present kernel weights generated through our optimal RD procedure, shown for
exposition for our main yields estimates results for low-rated issuers.
Figure A.6: Triangular Kernel Weights for Asymmetric Optimal Bandwidth, Effects on Yields
NOTES—Figure shows calculated triangular weights using asymmetric IMSE-optimal bandwidth on each side of
the cutoff for main yields estimate, as well as an alternative weighting scheme based on the regression coverage
error (CER), used for robustness. Weights and bandwidth are associated with the yields dependent variable in the
pooled city and county sample in the post-period.
In Table A.2, we further show sensitivity of our main result (column 1) to changing both bandwidth
selection method and the kernel used.
Table A.2: Sensitivity of Main Yields Results (A/BBB) to RD Kernel and Bandwidth Choice
(1) (2) (3) (4) (5) (6)
a. Pooled Post:
Overall Yield -19.42 -10.58 -11.73 -4.93 -15.80 -9.11
City Only -27.91 -7.34 -17.50 2.32 -25.79 -4.43
County Only -16.04 -20.78 -18.01 -23.72* -15.38 -22.19
High-Rated -1.75 -0.58 1.36 1.89 -1.45 -0.22
Low-Rated -75.43** -72.56* -66.64* -61.60* -76.24** -72.57*
b. Pooled Pre (Placebo):
Overall Yield -13.26 -5.34 -8.84 -2.21 -11.93 -4.96
City Only -9.34 -0.08 -5.90 3.56 -8.92 0.44
County Only -21.61 -15.94 -18.90 -12.77 -21.16 -15.46
High-Rated -6.09 -3.37 -5.02 -0.86 -6.00 -3.08
Low-Rated -25.14 -20.45 -26.38 -3.48 -25.54 -19.59
Bandwidth IMSE Fixed IMSE Fixed IMSE Fixed
Kernel TRI TRI UNI UNI EPN EPN
NOTES—Table presents RD estimate sensitivity of current yields (in basis points) for MSRB-active trades during
each sample period to different RD kernel and bandwidth choices. Each row corresponds to a separate regression
with that characteristic as the dependent variable. The discontinuity measures the jump in the regression function
at population eligibility 0 (relative to cutoff). IMSE: Integrated Mean-Squared Error; TRI: Triangular; UNI:
Uniform; EPN: Epanechnikov. State and calendar month fixed effects are included in all regressions. Standard
errors are clustered by population relative to the cutoff (the running variable), suppressed here for exposition. See
text for further sample restrictions. *** p≤0.01, ** p≤0.05, * p≤0.1.
A.9
A.7.4 Trade Seasonality and Composition
In Figure A.7, we present the seasonality of new issuance for a standard expansion year like 2019, which
demonstrates that effects on primary issuance are unlikely due to seasonal mean reversion in issuance.
Figure A.7: 2019 Seasonality in Primary Issuance
NOTES—Figure shows all CUSIPs tagged as new primary issuance based on initial offering date by calendar week
in 2019. Source: Mergent
In Figure A.8, we present the share of A/BBB trading bonds 100,000 in population above and below the
pooled cutoff that are general obligation (left) and revenue (right) bonds respectively. This plot shows
that while initial trading patterns support a spike in revenue bond trends when issuers were revealed
to be ineligible, this trend does not sustain. In conjunction with earlier work demonstrating balance,
composition differences across the cutoff immediately following the MLF announcement and unlikely
to be the main factor driving these results.
Figure A.8: Composition Sensitivity: GO and RB A/BBB Trends
NOTES—Figure shows shares of all trading CUSIPs for issuers 100,000 above and below the cutoffs.
A.7.5 Power Calculation for City Running Variable
In Table A.3 below, we provide power tests for various effect sizes to assess whether we can detect
reliable effect sizes (using the common convention of high power exceeding 0.80) for the 21 cities that
are above the 250,000 cutoff (along the city running variable).
A.10
Table A.3: Power Tests on City Running Variable (Cutoff = 250,000)
Level of Employment τ = 1, 000 τ = 2, 000 τ = 3, 000 τ = 4, 000
Employment, City Only Treated 0.10 0.27 0.53 0.78
– Services Employment, City Only Treated 0.11 0.29 0.56 0.81
Employment, City & County Treated 0.30 0.81 0.99 1.00
– Services Employment, City & County Treated 0.22 0.67 0.95 1.00
YoY Level Change in Employment τ = 100 τ = 200 τ = 300 τ = 400
Employment, City Only Treated 0.09 0.22 0.42 0.65
– Services Employment, City Only Treated 0.07 0.14 0.25 0.40
Employment, City & County Treated 0.16 0.47 0.81 0.97
– Services Employment, City & County Treated 0.12 0.33 0.63 0.87
YoY Percent Change in Employment τ = 1% τ = 2% τ = 3% τ = 4%
Employment, City Only Treated 0.10 0.25 0.48 0.72
– Goods Employment, City Only Treated 0.05 0.05 0.06 0.06
– Services Employment, City Only Treated 0.06 0.11 0.18 0.28
Employment, City & County Treated 0.20 0.61 0.92 0.99
– Goods Employment, City & County Treated 0.05 0.07 0.09 0.12
– Services Employment, City & County Treated 0.11 0.28 0.55 0.79
NOTES—We run power tests of our RD estimator for our city sample with a symmetric bandwidth of 250,000
in population using the rdpow and rdsampsi packages (Cattaneo et al. (2019b)). We omit the goods employment
rows in the first two panels because our detected RD effects are lower in magnitude than for services and overall
employment. Please see Cattaneo et al. (2019b) for more details. To perform the conventional power calculations
above, we assume there is ignorable “smoothing bias” on either side of the cutoff. We can therefore interpret these
calculations as upper bounds.
While we conclude from these results that only the largest effect sizes can be reliably estimated with full
power, for full transparency, we provide the corresponding RD estimation results in Table A.4 with this
caution in mind. To this end, we generate city employment as the county-weighted employment across
counties spanned by both eligible and ineligible cities. If one were to ignore power concerns and take
these results at face value, we are unable to detect any positive effects using this sample.
A.11
Table A.4: City-Level RD Estimates of MLF Access on Public Sector Employment
Emp. Emp. ∆ Emp. ∆ Emp. % ∆ Emp. % ∆ Emp. N
(1) (2) (3) (4) (5) (6) (fixed-bwdth)
a. Pooled Post:
Overall Employment -948 -1,045 -52 -49 -1.21 -0.56 29,609
(694) (781) (94) (94) (0.89) (0.72)
– Goods Employment -87** -113*** -1 0 -4.55 -2.29 5,370
(35) (41) (3) (3) (5.00) (4.35)
– Services Employment 1 -597 -98 -62 -1.01 0.37 19,669
(826) (943) (124) (120) (1.03) (0.74)
b. Pooled Pre (Placebo):
Overall Employment -740 -867 54** 52** 1.04*** 1.14*** 29,643
(725) (819) (24) (23) (0.40) (0.33)
– Goods Employment -83** -110*** -1 -1 0.22 -3.06 5,260
(35) (42) (2) (2) (3.12) (2.56)
– Services Employment 281 -229 69** 65** 0.86** 1.20*** 19,606
(880) (966) (28) (28) (0.42) (0.39)
Month FEs X
State FEs X X X
Control Mean (post): Employment 10,067 9,487 -779 -730 -6.64 -7.09
Control Mean (post): Goods Employment 154 134 -5 -4 -5.28 -4.92
Control Mean (post): Services Employment 8,555 8,022 -701 -653 -6.94 -7.75
NOTES—Table presents RD estimates of employment measure in column header and sample period. Each row
corresponds to a separate regression with that characteristic as the dependent variable. The discontinuity measures
the jump in the regression function at population eligibility 0 (relative to cutoff). The Control Mean denotes the
mean of that characteristic immediately to the left of relative population 0. Each regression uses a fixed bandwidth
with a triangular kernel to weight observations (see Section 4 for details). Percents in columns (5) and (6) range
from 0 to 100. Standard errors are conservatively clustered by population relative to the cutoff (the running
variable); as such, inference is drawn across unique issuers. *** p≤0.01, ** p≤0.05, * p≤0.1.
A.7.6 Full Baseline Summary Statistics
In Table A.5, we provide a full list of baseline summary statistics prior to March 23, including the entire
calendar year of 2019. These do not restrict to issuers within 100,000 of the cutoff, and instead are meant
to report endogenous differences between the samples of eligible and non-eligible issuers were they to
be compared naively, for example in a difference-in-differences analysis.
A.12
Table A.5: Full Baseline Summary Statistics, January 1, 2019 to March 23, 2020
MLF Eligible MLF Ineligible MLF Eligible - Ineligible
Mean/SD # Observations Mean/SD # Observations ∆/SE
(1) (2) (3) (4) (5)
A. MSRB-Bloomberg Trade-Level Data
Coupon Rate (b.p.) 430.3 669,311 384.2 844,395 46.2***
[135.1] [116.6] (0.21)
Security Price (per 100 par) 108.0 671,659 105.8 844,500 2.23***
[8.95] [7.45] (0.014)
Current Yield (b.p.) 203.0 620,560 209.6 825,352 -6.68***
[83.2] [80.3] (0.14)
∆ Yield (Feb20-Jan20) -0.066 281,596 -0.14 153,899 0.078***
[1.21] [0.95] (0.0033)
∆ Yield YoY (Jan20-Jan19) -0.89 262,725 -1.11 124,523 0.22***
[4.28] [1.17] (0.0090)
∆ Yield YoY (Feb20-Feb19) -1.00 242,935 -1.07 110,336 0.074***
[1.56] [1.07] (0.0045)
Amount Outstanding (MM) 2328.8 671,659 144.5 844,500 2184.3***
[2982.3] [224.1] (3.65)
Maturity Size (MM) 3542.0 671,659 215.7 844,500 3326.2***
[4209.3] [305.5] (5.15)
Tenor of Bond (Years) 14.8 671,464 13.2 844,500 1.55***
[7.64] [6.98] (0.012)
Remaining Duration of Bond (Years) 9.22 671,464 8.72 844,500 0.51***
[7.02] [6.74] (0.011)
Market Share of Issuer 0.95 671,659 0.064 844,500 0.89***
[1.06] [0.11] (0.0013)
Number of Securities by Issuer 306.4 671,659 123.0 844,500 183.3***
[210.6] [107.5] (0.28)
Par Traded (1000s) 290.9 671,659 95.4 844,500 195.5***
[1915.2] [579.9] (2.42)
S&P Ratings (1-7 scale) 5.67 575,172 5.83 624,205 -0.16***
[0.86] [0.65] (0.0014)
Moody’s Ratings (1-7 scale) 5.78 557,662 5.88 474,590 -0.099***
[0.90] [0.92] (0.0018)
Fitch Ratings (1-7 scale) 5.65 424,063 5.63 149,058 0.018***
[1.03] [0.79] (0.0026)
Time of Day of Trade (minute) 770.6 671,659 776.1 844,500 -5.53***
[131.7] [132.2] (0.22)
B. QCEW Month-County Loc. Gov. Emp. Data
∆ Employment 627.8 228 19.9 5,250 607.9***
[861.7] [99.5] (57.1)
∆ Goods Employment 9.77 130 0.20 2,402 9.57***
[35.4] [8.89] (3.11)
∆ Service Employment 1509.8 228 23.1 5,250 1486.7**
[10905.4] [414.9] (722.2)
NOTES—Table presents summary statistics for key variables of the analysis using a longer period prior to the first
Federal intervention in the municipal market, along with a two-sided t-test with heteroskedastic-robust standard
errors). See Appendix A.4 for further details on variable definitions and construction.
A.13
A.7.7 RD Effects on Credit Downgrade Probability
Here we explore the possibility that ratings agencies disproportionately downgraded issuers that
narrowly miss the cutoff (or do not downgrade issuers if supported by the MLF), and investors either
price MLF access similarly to NRSROs, or in response to them. While this is a very specific type of
credit risk measure, we expect it to be broadly correlated with default risk. Toward this end, we first
construct a balanced month-by-bond panel, and count how many times a bond received a downgrade
from any of the three major NRSROs relative to its rating in the previous month. Analogous to earlier
event study plots, in Figure A.9 we focus on the arbitrary symmetric bandwidth 100,000 in population
around each cutoff, and report cumulative downgrades separately by the underlying issuer’s plurality
rating in January 2020.
Figure A.9: Credit Rating Downgrades within 100k Population of MLF Eligibility Cutoffs
(a) Cumulative Downgrades, All Ratings (b) Cumulative Downgrades, Low-Rated (A & BBB)
NOTES—Panels (a) and (b) count the number of times a bond is downgraded relative to the prior month for
eligible issuers with cutoff-relative populations between 0 and 100,000 inclusively (blue dashed series), and issuers
with cutoff-relative populations greater than or equal to -100,000 and less than 0 (red solid series).
Panel (a) shows that independent of MLF eligibility, while the number of downgraded bonds moved
in tandem throughout April and May, by June of 2020, issuers that were revealed to be ineligible and
therefore without an emergency liquidity option (red solid series), were downgraded at a faster rate than
MLF-eligible issuers’ bonds. The number of MLF-ineligible issuer bond downgrades rose from roughly
100 to 600 by November of 2020, whereas downgrades were rarer for issuers that had MLF optionality.82
Panel (b) shows a noisier but related pattern among low-rated issuers: in August, low-rated ineligible
issuers began to experience more downgrades (rising to roughly 150 downgrades by November), and
accounted for about 25% of the aggregate downgrade pattern—a large share relative to the number
of total issuers and bonds that are in the sample. One interpretation for why there may have been
downgrades across the ratings distribution, but these were only priced into yields on the low end, is that
underlying mal-priced credit risk may be particularly exposed during a crisis for issuers that are closer to
the default margin. Both credit rating agencies (NRSROs) and private investors may have responded to
the newly revealed risks differently, depending on whether a given issuer had an emergency credit-risk
sharing option, such as access to the MLF.
While these patterns are striking, such rare events are difficult to detect statistically due to the
82 This pattern also persists when looking at the cumulative share of total bonds that are newly issued, which accounts for
concerns that effects may be mechanically related to a greater number of issuers below the cutoff.
A.14
majority of muni bonds exhibiting no change in ratings over the analysis period. In Table A.6 below, we
formalize this notion by estimating whether a bond was downgraded (relative to the previous month)
in the post-MLF or pre-MLF period, and how many bonds on average were downgraded during this
period. Similar to our analysis of primary issuance, here we collapse the data to two observations per
bond—one in the pre-MLF period and one in the post-MLF period.
Table A.6: RD Estimates of MLF Access on Credit Rating Downgrades
Discontinuity Standard Error Control Mean N (Fixed-bwdth)
a. Pooled Post:
Pr(Downgrade), Overall (may20-nov20) -0.02 0.04 0.06 142,155
Pr(Downgrade), A & BBB (may20-nov20) 0.06 0.15 0.15 12,132
Number of Downgrades, Overall (may20-nov20) -0.03 0.04 0.06 142,155
Number of Downgrades, A & BBB (may20-nov20) 0.06 0.15 0.15 12,132
b. Pooled Pre (Placebo):
Pr(Downgrade), Overall (jan20-feb20) -0.02 0.01 0.02 120,786
Pr(Downgrade), A & BBB (jan20-feb20) -0.05 0.04 0.05 10,313
Number of Downgrades, Overall (jan20-feb20) -0.02 0.01 0.02 120,786
Number of Downgrades, A & BBB (jan20-feb20) -0.05 0.04 0.05 10,313
NOTES—Table presents RD estimates of the probability that a bond was downgraded in the period of interest
(post-MLF or pre-MLF), and the number of downgrades each bond may have received in the same period. Each
row corresponds to a separate regression with that characteristic as the dependent variable. The discontinuity
measures the jump in the regression function at population eligibility 0 (relative to cutoff). The Control Mean
denotes the mean of that characteristic immediately to the left of relative population 0. Sample sizes vary
depending on the bandwidth used. Standard errors are clustered by population relative to the cutoff (the running
variable). See text for further sample restrictions. *** p≤0.01, ** p≤0.05, * p≤0.1.
While the table reveals that in the post-period, bonds of all ratings have negative coefficients
associated with a lower downgrade rate for eligible issuers, these cannot be detected statistically against
the vast majority of bonds that experience no change in ratings. For low-rated issuers, we in fact report
positive point estimates, which suggests that the number of downgrades among MLF eligible issuers
represented a larger share of total bonds than downgrades among ineligible issuers. Nevertheless,
neither is statistically different from zero, and both are estimated with noise. We thus cautiously interpret
these results in conjunction with the overall plots, as providing modest evidence that MLF-eligible
issuers had lower downgrade rates than observationally equivalent ineligible issuers.
A.15
A.8 Liquidity-Credit Risk Decomposition Details
In this section we discuss the various liquidity measures that enter our spreads decomposition. As with
our main cities and counties sample, we source municipal bond transaction-level prices and yields from
MSRB, but here extend our sample back to January 2013, which is the earliest date for which we have
transaction data that includes all three trade type indicators (i.e., D for interdealer trade, P for a dealer
purchase from a client, and S for a dealer selling to a client) to properly estimate liquidity measures. Each
trade record includes the trade time, bond price, yield, par value traded, and an indicator for whether the
trade was a customer purchase from a broker-dealer, customer sale to a broker-dealer, or an interdealer
trade. We follow the cleaning procedure of MSRB transactions data that is common in the literature
(see e.g., Green et al., 2010), and exclude bonds with missing coupon and maturity information (which
effectively removes variable rate bonds), a listed coupon greater than 20%, or a listed maturity over 100
years. These are likely to be data errors.
To mitigate the effect of outliers, we further remove CUSIPs that are traded less than 10 times
over the entire sample, trades that: occur on weekends and SIFMA holidays, have a price less than
50 or greater than 150, a when-issued flag equal to “Y”, a non-missing Brokers Broker Indicator, occur
within 90 days of issuance, and any trade date after the maturity date of the bond. Next, we use
bond characteristics from Bloomberg and Mergent’s Municipal Bond Securities Database, including
maturity, offering amount, coupon rate, state of issuance, issue series, issuance date, whether it was a
negotiated or competitive sale, whether the bond is general obligation, revenue, insured or callable, and
ratings from S&P, Moody’s, and Fitch, to further filter the data. We exclude variable rate bonds, insured
bonds, AMT bonds, and bonds that are only subject to federal taxes (for the decomposition), as these
characteristics will add noise to spreads. Table A.7 shows how each of these filters reduces the data to
our final baseline decomposition sample:
Table A.7: Decomposition Sample Construction
Number of Trades Number of Bonds
Full MSRB (01/2013-12/2020) 76,151,987 1,650,345
Clean MSRB 59,907,262 653,692
MSRB-Mergent merge 59,905,179 653,590
Exclude variable rate 58,748,919 648,723
Exclude insured bonds 45,575,328 476,877
Exclude AMT bonds 44,884,556 469,367
Exclude trades occurring [0,90 days] of issuance 41,056,328 462,386
Exclude bonds with time-to-maturity less than one year 38,888,523 453,988
Exclude insular areas 37,990,711 452,711
Keep State City and County issuers 8,052,129 157,259
City/County Baseline sample (2020 cal. year) 1,089,760 73,556
NOTES—Observation counts here are reported at the trade-level. As such, these counts will not align perfectly
with those in Table 6 in which we report mean-collapsed bond-week observations after calculating liquidity
measures on the disaggregated Baseline sample data.
Using this transactions sample, we estimate five measures of liquidity spread at the bond-week level.
First, we calculate each liquidity measure at the bond-day level and then we collapse to bond-week level
by taking the mean of the daily observations. Then, we use this set of liquidity measures as an input to
generate the first principal component of liquidity (our main metric of interest):
1. Amihud price impact
2. Effective Bid-Ask Spread
A.16
3. Imputed round-trip cost
4. Roll measure
5. Price dispersion
Each measure captures a different aspect of trading costs and is based on traded market prices rather
than quotes. While quotes might be available through Bloomberg or other sources, they are not binding,
and often only hold for small quantities or can be stale, due to the over-the-counter structure of the
municipal bond market, where prices are the result of bilateral negotiations between clients and dealers.
This market structure could also lead to situations when a bond is traded at significantly different prices,
at approximately the same time. Yet, the assumption that underlies all these measures is that the actual
trading is done mostly within the bounds of the quotes.
1. Amihud: Amihud (2002) is a low-frequency measure of the price impact of a trade, i.e., how much
the price moves per a $1 million trade. The Amihud measure for bond b on day t is calculated as:
Pj − Pj−1
1 Nt |r j | 1 Nt Pj−1
Amihudb,t = ∑
Nt j=1 Q j
=
Nt j∑ Qj
(7)
=1
where Nt is the number of trades on day t, Pj is the price of the bond at trade j, and Q j is the par amount
of trade j. We require at least two transactions on a given day to estimate the Amihud measure. Weekly
estimates of the Amihud measure are obtained by taking the mean of CUSIP-day estimates in a week,
and shown in Figure A.10.
Figure A.10: Amihud Evolution in Municipal Bond Markets
(a) Amihud since Great Recession (b) Amihud in 2020 Calendar Year
NOTES—Figure shows the weekly mean of the Amihud measure (the mean of CUSIP-days) over time for city and
county bonds by January plurality ratings.
2. Effective Bid-Ask Spread (BAS): The effective bid-ask spread is meant to capture dealer
compensation for the information advantage possessed by informed traders in a context of few buyers
and sellers at desired price ranges. We calculate the effective BAS for each bond as the difference between
the size-weighted buy price within the week and the size-weighted sell price within the week, divided
by the midpoint of the two prices (adjusting for heterogeneous mark-ups by price levels). Specifically:
A.17
B pB − S pS
∑n∈bt wnbt nbt ∑n∈bt wnbt nbt
BASbt = B pB + S pS )
. (8)
0.5 × (∑n∈bt wnbt nbt ∑ w
n∈bt nbt nbt
Figure A.11 plots the weekly time-series of the average effective bid-ask spread (BAS) across all city and
county bonds, separately by January 2020 plurality ratings.
Figure A.11: Bid-Ask Spread Evolution in Municipal Bond Markets
(a) BAS since Great Recession (b) BAS in 2020 Calendar Year
NOTES—Figure shows the average effective bid-ask spread over time for city and county bonds. We calculate the
effective bid-ask at the bond-week level as the volume-weighted difference between transacted buy price and sell
price from the client’s perspective, adjusted by the midpoint level of the two prices. We show results separately
by January 2020 issuer plurality ratings, as discussed in the text.
3. Imputed Round-trip Cost (IRC): Similar to the effective BAS, imputed round-trip costs also capture
the degree of liquidity in the market, but also include direct transaction costs such as commissions or
fees. Following Feldhütter (2012), we identify imputed round-trip trades for a given bond on a given
day if there are exactly two or three trades for a given volume that occur within fifteen minutes. Those
trades are likely a part of a pre-matched arrangement in which a dealer has matched a buyer and seller.
In an imputed round-trip trade, the highest price is assumed to be an investor buying from a dealer,
while the lowest price assumed to be an investor selling to a dealer. The investor round-trip cost for
bond b and day t is then calculated as the highest minus the lowest price. Specifically:
Pmax − Pmin
IRCbt = (9)
Pmin
where Pmax is the highest price and Pmin is the lowest price in an imputed round-trip trade. Weekly IRC
estimates at the bond-level are obtained by taking the mean of daily estimates in a given week, and are
shown in Figure A.12.
A.18
Figure A.12: Imputed Round-Trip Costs in Municipal Bond Markets
(a) IRC since Great Recession (b) IRC in 2020 Calendar Year
NOTES—Figure shows the average imputed round-trip cost over time for city and county bonds, separately by
January 2020 plurality ratings.
4. Roll Measure: Roll’s measure (Roll (1984)) provides an alternative construction of the BAS,
but requires two strong assumptions. First, the market is informationally efficient. Second, the
probability distribution of observed price changes is stationary (at least for short intervals). Under
these assumptions, if trading costs are zero, a change in price will occur if and only if unanticipated
information is received by market participants. There will be no serial dependence in successive price
changes (aside from that generated by serial dependence in expected returns). However, if trading is
costly, the dealer will be compensated by the bid-ask spread. When information arrives, both the bid
and the ask prices move to different levels such that their average is the new equilibrium value. Thus,
the bid-ask average fluctuates randomly in an efficient market. Observed market price changes are no
longer independent because recorded transactions occur at either the bid or the ask, not at the average,
and a negative serial dependence in observed price changes should be anticipated.
In our context, we calculate the Roll measure for bond b and day t as:
q
Rollbt = 2 × −Cov (∆Pn , ∆Pn−1 ) (10)
where Pn is the price at trade n and the measure is set to zero when the covariance between successive
price movements is positive. We estimate the Roll measure on each day there is at least one trade, using
a trailing 30-day window. Weekly estimates of the Roll measure are obtained by taking the mean of the
daily estimates in a week.
A.19
Figure A.13: Roll Measure in Municipal Bond Markets
(a) Roll Measure since Great Recession (b) Roll Measure in 2020 Calendar Year
NOTES—Figure show the weekly mean Roll Measure over time for city and county bonds, separately by January
2020 plurality ratings.
5. Price Dispersion: We also consider an alternative measure following Jankowitsch et al. (2011), who
use the wedge between expected and traded prices to estimate liquidity. We calculate the dispersion of
traded prices around a market “consensus valuation”. While this measure is similar to the other liquidity
measures, it is not perfectly correlated and seems to contribute additional information about the market
liquidity. So, for each bond b on day t we calculate:
v
u ! −1
u Nbt Nbt
Dispersionbt = t
∑ Qbn ∑ ( Pbn − Mbt ) Qbn
2
(11)
n =1 n =1
where Nbt is the number of trades of bond b on day t, Pbn is the price of the bond at trade n, Qbn is the
par amount of trade n, and Mbt is the market “consensus valuation” for bond b, which is calculated as
the daily volume-weighted average price of the bond. Weekly estimates of the price dispersion measure
at the bond-week level are obtained by taking the mean of the daily estimates in a week, and are shown
in Figure A.14.
A.20
Figure A.14: Price Dispersion Measure in Municipal Bond Markets
(a) Price Dispersion Measure since Great Recession (b) Price Dispersion Measure in 2020 Calendar Year
NOTES—Figure shows the average weekly Price Dispersion measure over time for city and county bonds,
separately by January 2020 plurality ratings.
Choice of Liquidity Measures: In the main text we choose to present results using a liquidity factor
that is calculated based on only four illiqudity measures, excluding the bid-ask spread. Given the
relationship between transaction costs and trade size, we would have liked to compare buy and sell
prices of trades with similar sizes. As Green et al. (2010) has observed, dealers often provide liquidity to
institutional traders by purchasing large blocks of bonds and selling smaller blocks off to retail investors,
or to regional dealers with retail distribution capability. This results in asymmetry of the trade size of
buys and sales. A reasonable condition such as requiring at least one buy and one sale, each with a
trade size greater than $100,000 results in a very restrictive sample, as shown in Figure A.15. Relaxing
this restriction indeed results in a similar coverage of bonds as the other illiquidity measures, but we
prefer not to use a measure that “mixes” transaction costs of large and small trades without properly
“controlling” for the trade size (as the IRC does for example). In either case, our results are robust to
including or excluding BAS, and to including BAS without the >$100,000 restriction.
To illustrate the number of bonds that contribute to each measure in a given week, Figure A.15 shows
the number of distinct CUSIPs that are in our Baseline sample each week, both overall, and by measure.
A.21
Figure A.15: CUSIP Coverage of Each Illiquidity Measure
Summary of Liquidity Measures and Liquidity First Principal Component Method: The different
illiquidity measures above capture the expected transaction costs and the risk of these costs changing.
Historically, as expected, we observe that lower rated bonds (A and BBB) are less liquid than higher
rated bonds (AAA and AA).
Table A.8 summarizes the distributive properties of the four illiquidity measures used for the
analysis. While the measures are correlated, each individual measure still contains additional distinct
information, as observed in Table A.9 which reports the correlation between measures. We also observe
that transaction costs are high, though liquidity in the market has been improving over the past decade.
We normalize each liquidity measure by subtracting its mean and dividing by its standard deviation
over the sample period (January 2013 - December 2020):
Lkbt − µb
λbt = ,
σb
where Lkbt is one of the liquidity measures k (Amihud, BAS, IRC, Roll, or Price Dispersion) for bond b on
week t. We then consider the first principal component of the four liquidity measures (excluding BAS)
as the liquidity factor λbt . When we present the results for the calendar year 2020, we restrict the sample
only after following the procedure described above. That is, the weekly liquidity factors are based on
normalization that is based on a longer time series, from January 2013 to December 2020.
Figure A.16 plots the first principal component of the four normalized illiquidity measures. Panel
(a) shows the time series of average illiquidity variable λt from 2013 to 2020, exhibiting a long term
improvement in liquidity in the municipal bond market consistent with evidence in the literature (e.g.,
Wu, 2018). Panel (b) takes a closer look at the liquidity during 2020. We see that liquidity worsened in
early March during COVID-19 market dislocation across all rating groups. While AAA/AA liquidity
improved post-MLF announcement and other Federal interventions that were introduced between
mid-March and the end of April 2020, liquidity of the lower rated bonds (A and BBB) has continued
to be a problem throughout 2020.
A.22
Table A.8: Illiquidity Measures Summary Statistics. This table reports summary statistics for the
bond-week illiquidity measures.
Mean SD p1 p10 p50 p90 p99 # Observations # Bonds
Amihud (% per $1m) 26.8 48.9 0 0 7.63 75.7 256.7 2,117,126 156,925
BAS 0.44 0.61 0 0.016 0.18 1.33 2.69 187,215 154,322
IRC (%) 0.69 0.70 0.030 0.090 0.42 1.80 2.81 1,670,714 156,933
Roll 1.14 1.21 0 0 0.76 2.83 5.22 907,800 130,840
Dispersion 0.29 0.34 0 0 0.13 0.85 1.36 2,123,759 66,884
Table A.9: Correlations between Illiquidity Measures. This table reports correlations between
illiquidity measures on a weekly basis.
Amihud BAS IRC Roll Dispersion
Amihud 1 0.2360 0.4220 0.3642 0.4704
BAS 0.2360 1 0.7296 0.4170 0.8203
IRC 0.4220 0.7296 1 0.4987 0.8372
Roll 0.3642 0.4170 0.4987 1 0.5227
Dispersion 0.4704 0.8203 0.8372 0.5227 1
Figure A.16: First Principal Components This figure plots the first principal component of illiquidity
measures on a weekly basis, calculated separately for cities and counties by January 2020 plurality
ratings.
(a) First PC since Great Recession (b) First PC in 2020 Calendar Year
A.23
Figure A.17: Illiquidity and Credit Risk Evolution in the 2020 Municipal Bond Market, Including States
(a) States + CC, AAA/AA (b) States + CC, A/BBB
NOTES—Panels (a) and (b) show the weekly averages of the default and liquidity components of city, county, and
state bond yields by ratings group for each week in the 2020 calendar year.
A.24
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