Ambulance Taxis: Eliason, League, Leder-Luis, McDevitt & Roberts (2025)

What this is. This is a distilled skeleton of Eliason, League, Leder-Luis, McDevitt, and Roberts (2025). Read the original paper or the NIH Public Access version to replicate or extend.

TL;DR

Between 2003 and 2017, Medicare spent $7.7 billion on 37.5 million nonemergency ambulance rides transporting dialysis patients to and from treatment facilities, many of which did not satisfy Medicare’s medical necessity criteria. Using the staggered rollout of a prior authorization requirement across US states and the differential timing of 69 criminal and civil DOJ lawsuits across 26 federal judicial districts, the paper identifies the causal effects of two anti-fraud approaches. Prior authorization, which requires ambulance companies to obtain physician sign-off before providing a ride and receiving payment, caused an immediate and persistent 68% drop in nonemergency rides. Criminal litigation reduced rides by roughly 24%, while civil litigation had no statistically significant effect. No evidence is found that prior authorization harmed patient health. The paper estimates the federal government would have saved $4.8 billion had it imposed prior authorization in 2003 at an administrative cost of only $28.6 million per year.

Core results

#	Result	Locator	Magnitude as reported
R1	Prior authorization reduces total Medicare payments for nonemergency dialysis rides	Table 2, col. 1, p. 1676	beta = -1.129 log points (SE = 0.350)**, dep. mean = 9.934; -67.7% in levels
R2	Prior authorization reduces total nonemergency ride count	Table 2, col. 3, p. 1676	beta = -0.913 log points (SE = 0.176)***, dep. mean = 5.357
R3	Criminal enforcement reduces total ride payments (modest, delayed)	Table 3, col. 3, p. 1678	beta = -0.211 log points (SE = 0.106)+; Fig. 5 shows gradual decline over 24 months
R4	Criminal enforcement reduces ride count	Table 3, col. 4, p. 1678	beta = -0.280 log points (SE = 0.099)**
R5	Civil enforcement has no significant effect on payments	Table 3, col. 1, p. 1678	beta = -0.042 (SE = 0.110), n.s.
R6	Civil enforcement has no significant effect on ride count	Table 3, col. 2, p. 1678	beta = 0.026 (SE = 0.066), n.s.
R7	Prior authorization reduces number of active ambulance firms by 24.9%	Table 6, col. 1, p. 1681	beta = -0.286 log points (SE = 0.066)***, dep. mean = 2.152
R8	No evidence of adverse patient health effects from prior authorization	Table 4, p. 1680; Table 5, p. 1680	mortality: 0.000372 (SE 0.000580) n.s.; dialysis sessions: -0.026 (SE 0.019) n.s.; hospitalizations: -0.00132 (SE 0.00136) n.s.
R9	Dialysis ambulance use was frequent among riders	Table 1, p. 1671; text p. 1670	Riding patient-months averaged 19.54 nonemergency rides; riders averaged 660.3 lifetime claims; the study covers 37.5 million rides and over $7.7 billion in spending
R10	Payment effects were similar across the two authorization rollout waves	text p. 1676	First wave: -1.21 log points; second wave: -1.07 log points; difference not statistically significant
R11	Prior authorization did not reduce emergency ambulance rides, a falsification outcome	text p. 1676	The appendix F falsification test reports no impact on emergency rides; the main text gives no coefficient
R12	Frequent riders also show no detectable health deterioration after authorization	Table 5, p. 1680	Dialysis sessions: -0.0226 (SE 0.0312); mortality: -0.000433 (SE 0.00167); all-cause hospitalizations: -0.00828 (SE 0.00517); fluid hospitalizations: -0.00137 (SE 0.00176), all n.s.
R13	Authorization changed the ambulance-firm market and increased specialization	Table 6, p. 1681; Figure 7, p. 1683	Active firms: -0.286 log points (SE 0.0657)***; firms serving only nonemergency dialysis rides rose from 93 to 120; over half of firms with under 20% nonemergency rides exited (text p. 1683)
R14	Remaining riders were less persistent and more medically acute	Table 7, p. 1684	Among riding patient-months: next-month ride probability -0.0633 (SE 0.0529); same-month hospitalization +0.01171 (SE 0.00630); same-month mortality +0.00711 (SE 0.00348)*
R15	Claim denials rose after authorization, consistent with screening	Figure 10, p. 1686; text p. 1695	Overall claim denial rate: 5.7% in the year before authorization to 22.7% in January 2015; firms exiting at the start rose from 8.1% to 52.5%
R16	Litigation barely changed the market-wide number of active firms	Table 8, p. 1687	Civil: log firms +0.0122 (SE 0.0290), count +0.779 (SE 0.652); criminal: log firms -0.0442 (SE 0.0731), count -5.651 (SE 6.436)
R17	Criminal indictments incapacitated defendants, unlike civil complaints	Figure 12, p. 1688; text p. 1688	Payments fell nearly to zero after criminal indictments; text estimates an approximately $12,000 per firm-month decrease in the observed 20% sample, about $60,000 scaled to all claims; civil cases had no apparent effect
R18	Greater DOJ enforcement capacity did not measurably change rides or payments	Table 9, p. 1689	Civil hours: payment +0.0117 (SE 0.105), rides -0.0124 (SE 0.0574); criminal hours: payment +0.0631 (SE 0.191), rides -0.0705 (SE 0.144); total hours: payment +0.102 (SE 0.262), rides -0.0478 (SE 0.196)
R19	The full-sample counterfactual implies large fiscal savings	Conclusion, text p. 1698	Authorization throughout the sample would save $4.8 billion, prevent 21.2 million unnecessary rides, and cost about $28 million per year to administer
R20	Litigation effects were localized, supporting the district comparison design	text p. 1676	Appendix G reports no negative impacts on rides or payments in neighboring districts; exact estimates are not reported in the main text

Overall (paper’s conclusion). Prior authorization was far more effective than pay-and-chase litigation for reducing Medicare ambulance fraud because it prevents fraudulent payments from being made in the first place, bypassing the twin obstacles of limited defendant liability and low prosecution probability that make realized enforcement ineffective against a large population of small fraudulent firms.

Theory / model

Section VI frames why prior authorization can outperform litigation when fraudulent providers can spend proceeds before enforcement, penalties are limited by recoverable assets, and detection is unlikely (pp. 1690-1693). The firm’s fraud decision is equation (5):

The model builds on Shavell (1984) and Polinsky and Shavell (2000) on liability and public enforcement, Becker (1968) on crime and punishment, and Glaeser and Shleifer (2003) on when administrative rules outperform litigation. The regulation-versus-investigation comparison also relates to Behrer et al. (2021).

$$G(\text{Reg}) > P_{\text{Crim}} F_{\text{Crim}} + P_{\text{Civ}} F_{\text{Civ}} \tag{5}$$

The gain from fraud is revenue less operating cost, while prior authorization raises compliance costs and reduces revenue through denials (text p. 1690):

$$G(\text{Reg}) = R(\text{Reg}) - C(\text{Reg})$$

Penalties reflect treble damages capped by assets, with jail disutility added for criminal enforcement (text p. 1690):

$$F_{\text{Civ}} = \min(3R(\text{Reg}),\, \text{Assets}), \qquad F_{\text{Crim}} = \min(3R(\text{Reg}),\, \text{Assets}) + J$$

The mechanism is that limited liability caps collectible monetary penalties, and low detection probability keeps expected litigation costs low. In 27 prosecution cases with recovery data, recovered funds averaged less than $1.2 million or 51% of amounts owed (text p. 1691). From 2007 to 2014, the authors estimate 2.4% criminal and 3.8% civil enforcement probabilities, based on 28 criminal and 44 civil defendants relative to about 1,150 potentially fraudulent firms (text p. 1692). Prior authorization directly lowers the expected gains by preventing claims from being paid until medical necessity is approved. The observed denial rate rose from 5.7% before authorization to 22.7% in January 2015 (text p. 1695).

Method

The design uses the staggered rollout of prior authorization across states and staggered timing of DOJ civil and criminal actions across federal judicial districts. Prior authorization began in December 2014 in New Jersey, Pennsylvania, and South Carolina, with a second wave in January 2016. Lawsuit treatment dates are the first filing of the relevant action in each district (Section IV, pp. 1673-1675). The main design is a two-way fixed effects event study and a scalar post-treatment summary, with district and month fixed effects and controls for prior exposure to other enforcement types. Treatment windows are restricted to districts observed for the full event window: K=24 pre-treatment months and L=23 post-treatment months for district outcomes, and K=12, L=11 for patient outcomes (pp. 1673-1674). Standard errors are clustered by district.

The district-level event study is equation (1), with the month immediately before treatment omitted as the reference period (p. 1673):

$$Y_{dt} = \sum_{e=-K}^{-2} \beta_e T_{dt}(e) + \sum_{e=0}^{L} \beta_e T_{dt}(e) + \alpha_d + \alpha_t + \Gamma X_{dt} + \epsilon_{dt} \tag{1}$$

Equation (2) replaces the post-treatment event-time coefficients with their common average, representing the average effect over the first L months (pp. 1673-1674):

$$Y_{dt} = \sum_{e=-K}^{-2} \beta_e T_{dt}(e) + \beta \sum_{e=0}^{L} T_{dt}(e) + \alpha_d + \alpha_t + \Gamma X_{dt} + \epsilon_{dt} \tag{2}$$

For patient-level outcomes, equations (3) and (4) use the same dynamic and scalar specifications, with patient and facility controls and a one-year event window (p. 1674):

$$Y_{idt} = \sum_{e=-K}^{-2} \beta_e T_{dt}(e) + \sum_{e=0}^{L} \beta_e T_{dt}(e) + \alpha_d + \alpha_t + \Gamma X_{idt} + \epsilon_{idt} \tag{3}$$ $$Y_{idt} = \sum_{e=-K}^{-2} \beta_e T_{dt}(e) + \beta \sum_{e=0}^{L} T_{dt}(e) + \alpha_d + \alpha_t + \Gamma X_{idt} + \epsilon_{idt} \tag{4}$$

Appendix B reports alternative staggered difference-in-differences estimators; Appendix D varies control groups and functional forms. The main text reports those checks as consistent with the principal estimates (pp. 1674-1675, 1676).

Empirical specifications

District-level rides and payments (Tables 2-3, pp. 1676, 1678). Equation (2) is estimated on log(1 + payments) and log(1 + rides), as well as levels. The policy treatment is prior authorization for Table 2 and the first civil or criminal action in the district for Table 3. District and year-month fixed effects are included, along with controls for exposure to other enforcement types; standard errors are clustered by district. Table 2 uses 7,272 district-months from 2011-2017. Table 3 uses 14,160 civil and 14,436 criminal district-month observations from 2003-2017. Table 2 estimates -1.129 (SE 0.350) for log payments and -0.913 (SE 0.176) for log rides. Table 3 estimates civil effects of -0.042 (SE 0.110) on log payments and +0.026 (SE 0.0663) on log rides, and criminal effects of -0.211 (SE 0.106) and -0.280 (SE 0.0994), respectively.

Patient health and selection (Tables 4-5, pp. 1680; Table 7, p. 1684). Equations (3)-(4) estimate patient-month outcomes from 2011-2017 with district and year-month effects, patient and facility controls, facility fixed effects, and district-clustered standard errors. Table 4 has 15,077,158 patient-months; Table 5 restricts to frequent riders with at least 100 rides before the policy and has 905,331 observations. Table 7 restricts to current rider-months and has 603,917 observations. The health outcomes in Tables 4-5 are dialysis sessions, mortality, all-cause hospitalization, and fluid hospitalization. Table 7 estimates next-month riding and same-month hospitalization and mortality, measuring post-policy changes in who continues to use rides rather than average health effects across all patients.

Firm outcomes and litigation incapacitation (Tables 6 and 8, pp. 1681, 1687; Figure 12, p. 1688). Equation (2) is estimated for log(1 + active firms) and active-firm counts, with district and year-month fixed effects and standard errors clustered by district. Table 6 uses 6,336 district-months from 2012-2017 in the USRDS data. Table 8 uses the 20% Medicare claims sample, 12,143 civil and 12,203 criminal district-month observations from 2007-2019. Figure 12 follows firm-month payments around the complaint or indictment date. The paper reports the firm-level criminal-incapacitation contrast descriptively: payments fall nearly to zero after indictment, while civil complaints show no apparent effect; the text scales the criminal payment reduction to about $12,000 monthly in the 20% sample.

Patient selection and claim screening (Table 7, p. 1684; Figure 10, p. 1686). Table 7 estimates equation (4) for current rider-months, with patient and facility controls, facility fixed effects, and district-clustered standard errors. Figure 9 presents the corresponding event-study path using equation (3), with K=12 and L=11. Figure 10 plots the share of submitted ambulance claims denied by Medicare across the two authorization waves. Its plotted claim-denial series is descriptive; no separate regression is specified in the main text.

Enforcement capacity (Table 9, p. 1689). The paper regresses log(1 + rides) and log(1 + payments) on log personnel hours devoted to civil, criminal, or total court cases, including district and month-year fixed effects. There are 1,410 district-month observations, and standard errors are clustered by district. The estimating specification represented by Table 9 is:

$$\log(1+Y_{dt}) = \theta \log(\text{CourtHours}_{dt}) + \alpha_d + \alpha_t + \epsilon_{dt}$$

where each column uses civil, criminal, or total court hours and Y is payments or rides. The six coefficients are small and statistically insignificant (Table 9, p. 1689). The paper also reports no negative spillovers to neighboring districts and no emergency-ride response as identifying and falsification checks (text pp. 1676).

Datasets used

Dataset	Role in paper	Wiki page
USRDS (United States Renal Data System), 100% Medicare ESRD sample	Primary outcome data: 37.5 million nonemergency ambulance rides billed to Medicare for dialysis patients, 2003-2017; patient demographics, comorbidities, dialysis treatment histories, facility identifiers	no page yet
DOJ litigation data (hand-collected)	Novel dataset of 69 lawsuits (43 criminal, 26 civil) against ambulance companies for dialysis fraud, 2003-2017; court records from PACER, press releases from DOJ; includes filing dates, jurisdictions, defendant names	no page yet
Medicare 20% sample, all beneficiaries	Firm-level outcomes (active firm count, incapacitation effects); 2007-2019; supplements USRDS which began recording firm identifiers only in 2012	no page yet
DOJ National Caseload Data	Enforcement capacity: log personnel hours of US Attorneys’ Offices devoted to civil and criminal cases by district-year, 2001-2021; used for general deterrence test (Table 9)	no page yet
FOIA responses on financial recoveries	Actual financial recoveries from 27 ambulance fraud prosecutions; obtained via Freedom of Information Act requests to US Attorneys’ Offices; average recovery $1.2 million (51% of penalties owed)	no page yet

Sample scope: US, 2003-2017 (main), 2007-2019 (firm-level). Unit of observation: district-month (main), patient-month (health outcomes), firm-month (incapacitation). Monthly frequency. The dialysis industry context draws on Eliason et al. (2020), who document how acquisitions by large chains affect dialysis facility behavior.

When to read the full paper

Read this paper if you are studying: (1) the empirical effectiveness of administrative regulation versus ex post litigation for deterring financial fraud, using a setting with clean staggered quasi-random variation in both; (2) Medicare fraud in the dialysis sector, including Table 1 (p. 1671) for patient summary statistics and Figure 1 (p. 1669) for the time series of rides; (3) the identification and robustness literature on staggered DiD, including comparisons with Callaway and Sant’Anna (2021) estimators (Appendix B); or (4) the economic theory of why limited liability and low detection probability undermine pay-and-chase enforcement (Section VI, pp. 1690-1696). The counterfactual savings calculation ($4.8 billion at $28.6 million/year administrative cost) is in Appendix K (p. 1698).

Attribution and rights

This page is a LLM-distilled summary, not human-verified, and not a reproduction of the research.

Eliason, P., League, R., Leder-Luis, J., McDevitt, R. C., and Roberts, J. W. (2025). “Ambulance Taxis: The Impact of Regulation and Litigation on Health-Care Fraud.” Journal of Political Economy 133(5): 1661-1702. https://doi.org/10.1086/734134

Paywalled (c) 2025 The University of Chicago. All rights reserved. Published by the University of Chicago Press. An NIH Public Access accepted manuscript is available at https://pmc.ncbi.nlm.nih.gov/articles/PMC12331087/. Replication data and code: Harvard Dataverse, https://doi.org/10.7910/DVN/QAGBDM. Extract-only: do not reproduce tables or figures without permission from the University of Chicago Press.