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. Author manuscript; available in PMC: 2026 May 1.
Published in final edited form as: Health Econ. 2025 Jan 31;34(5):815–820. doi: 10.1002/hec.4944

Drug Decriminalization and Fatal Traffic Crashes: Evidence from BM110 in Oregon

Christian Gunadi 1,*, Yuyan Shi 1
PMCID: PMC11961312  NIHMSID: NIHMS2055627  PMID: 39888329

Abstract

Background:

Oregon Ballot Measure 110 (BM 110) reduced the penalties for non-commercial possession of a controlled substance from a felony or misdemeanor to a new Class E violation, punishable with a $100 maximum fine. We sought to examine whether BM 110 was associated with changes in drug-related fatal traffic crashes in Oregon following its implementation in February 2021.

Methods:

This repeated cross-sectional study used Fatality Analysis Reporting System (FARS) 2018–2021 data to obtain population-adjusted state-level drug-related fatal traffic crashes. A modified version of a synthetic control method was utilized to create a “synthetic” Oregon that best resembled pre-policy sociodemographic characteristics and outcome trends in Oregon while also correcting for time-invariant pre-policy differences.

Results:

BM 110 was not associated with changes in drug-related fatal traffic crashes per 100,000 population (0.114, 95% CI: −0.106, 0.334).

Conclusion:

Early evidence indicates that BM 110 did not change drug-related fatal traffic crashes in Oregon after its implementation in February 2021.

INTRODUCTION

The United States has the highest number of incarcerated individuals in the world, with more than 2 million individuals imprisoned as of 2021 (Fair and Walmsley 2021). A significant portion of these incarcerations is due to drug-related offenses, where one in five incarcerated individuals is serving time for drug charges (Sawyer and Wagner 2023). Annually, arrests for drug possession outnumber those for drug sales by a factor of six (Sawyer and Wagner 2023). This high rate of incarceration reflects the stringent criminalization of illicit drugs in many states. (Travis, Western et al. 2014, EJI 2024).

Harsh drug sentencing has raised numerous concerns on social and public health issues, including the disproportionate impact on marginalized communities and the potential for worsening health and mental health among incarcerated individuals (Travis, Western et al. 2014, Pew 2018, Anderson and Olson 2020, EJI 2024). Critics argue that the punitive approach to drug offenses fails to address the underlying issues of addiction and can exacerbate societal harms (Travis, Western et al. 2014, Pew 2018, EJI 2024). In recent years, a global trend toward decriminalization has emerged, with many jurisdictions rethinking their policies on illicit substances (Alliance 2015). In the U.S., several states have begun to follow suit, reflecting a growing recognition of the limitations of punitive drug laws (Manz 2021).

In November 2020, Oregon voters passed Ballot Measure 110 (BM 110), which represents a significant shift in drug policy. Effective February 2021, BM 110 reclassified the possession of small amounts of controlled substances from a criminal misdemeanor to a Class E violation, subject to a maximum fine of $100. This measure also allocates funding for drug addiction treatment and recovery programs, supported by the state’s cannabis tax revenue and savings from reduced incarceration costs. However, it is important to note that these treatment programs were not fully funded until late 2022, highlighting a delay in implementation (Russoniello, Vakharia et al. 2023).

The literature on drug decriminalization indicates various impacts, including reductions in drug possession arrests and shifts in substance use patterns. For instance, several studies show that cannabis decriminalization has led to significant declines in possession arrests (Plunk, Peglow et al. 2019, Gunadi and Shi 2022, Gunadi and Shi 2022), and another study shows that cannabis decriminalization was associated with reductions in opioid-related deaths (Sabia, Dave et al. 2021). While these findings are promising, they primarily focus on cannabis, leaving a gap in understanding the broader implications of decriminalizing all illicit drugs.

Specifically, studies examining the impacts of Oregon’s decriminalization under BM 110 are limited. Initial evidence suggests that drug possession arrests have decreased in Oregon since the implementation of BM 110 (Davis, Joshi et al., 2023), and a study indicates an increase in unintentional drug overdose deaths following the measure (Spencer, 2022). However, comprehensive analyses of how BM 110 affects drug-related traffic fatalities and other public health outcomes are lacking.

This study aims to fill the gap in the literature by examining the impacts of Oregon’s drug decriminalization on drug-related fatal traffic crashes.1 Our research design utilizes a robust methodology that combines synthetic control with difference-in-differences. This approach creates a comparison group that closely resembles Oregon’s pre-policy outcome trends and characteristics, while also eliminating the influence of pre-policy time-invariant differences. By focusing on the effects of decriminalizing virtually all illicit substances, this study offers unique insights into the broader implications of such policies and their potential effects on public health and safety. The findings could have important policy implications, informing future decisions regarding drug laws in Oregon and beyond.

METHODS

Data Source

The monthly data on drug-related fatal traffic crashes were obtained from Fatality Analysis Reporting System (FARS) 2018–2021. Two criteria must be fulfilled for a traffic crash to be included in FARS (National Highway Traffic Safety Administration 2014). First, it must involve a motor vehicle traveling on a traffic way customarily open to the public. Second, it had to result in the death of at least one person within 30 days of the crash. For each qualifying traffic crash, FARS documents information on the circumstances, total fatalities, and demographics of the vehicle’s driver and its passenger. If drug tests were administered, information about the results of the tests was also reported. Drug-related fatal crashes were defined as traffic crashes resulting in fatalities in which one or more drivers involved in the incident tested positive for drugs.

Outcome Measures

We analyzed one outcome measure aggregated at the state level: drug-related fatal traffic crashes per 100,000 population per month. The state-level population estimates used for normalization were obtained from the Integrated Public Use Microdata Series (IPUMS) monthly Current Population Survey (CPS) (Flood, King et al. 2022).

Predictor Variables in the Construction of Synthetic Control

We used the monthly CPS obtained from IPUMS (Flood, King et al. 2022) to construct aggregate state-level sociodemographic characteristics, which included unemployment rate (%), proportion of population aged 20 or below (%), proportion of Hispanic individuals (%), proportion of non-Hispanic Black individuals (%), proportion of non-Hispanic minorities (%), and proportion of population with a high school diploma or less (%). Because using the entire pre-policy path of the outcome variable as predictors would render all other covariates irrelevant,(Kaul, Klößner et al. 2015) we only use the odd months in the pre-BM 110 period outcomes as predictors.

Statistical Analysis

To identify the changes in the outcomes following BM 110 in Oregon, a comparison group that can be used as a counterfactual of what would have occurred in Oregon in the absence of BM 110 is required. The usual approach is to use the rest of the U.S. jurisdictions to obtain the counterfactual. However, because the rest of the U.S. jurisdictions are likely to have different pre-policy outcome trends as well as sociodemographic characteristics compared to Oregon, an arguably better approach is to construct a “synthetic” comparison group in the spirit of Abadie et al.(Abadie, Diamond et al. 2010, Abadie, Diamond et al. 2015). Specifically, in this study we constructed the synthetic Oregon as a weighted combination of 31 jurisdictions in the donor pool (Supplemental Table S1). Washington was excluded from the donor pool to avoid potential bias from the state supreme court decision. In February 2021, the Washington Supreme Court struck down the state law that made drug possession a felony. As a response, the lawmakers passed a temporary law, effective July 2021 and set to expire on July 1, 2023, that makes possession of a small amount of drugs a misdemeanor offense while they are working on a long-term fix. The other jurisdictions were excluded from the donor pool due to implementing cannabis decriminalization, recreational cannabis legalization, or medical cannabis legalization during the study period. The weights were constructed to minimize the mean squared differences in the sociodemographic characteristics and outcome trends between the actual and synthetic Oregon prior to BM 110. These weights were restricted to the [0, 1] interval (Abadie 2021).

If there is a long enough pre-policy period and sociodemographic characteristics and outcome trends of the treatment state (Oregon) can be reasonably fitted by its synthetic comparison, the difference in the outcomes between the treatment states and its synthetic comparison can be interpreted as the effects of the policy (Abadie, Diamond et al. 2010). However, if the pre-policy fit is suboptimal and the differences in pre-policy outcomes and sociodemographic characteristics between the treatment state and its synthetic comparison did not vary with time, a difference-in-differences adjustment can be used to correct the estimates (Kreif, Grieve et al. 2016). Therefore, we follow recent works to combine the synthetic control method and the traditional difference-in-differences method to eliminate the influence of pre-policy time-invariant differences (Bohn, Lofstrom et al. 2014, Courtemanche and Zapata 2014, Kreif, Grieve et al. 2016, Ryan, Krinsky et al. 2016). Specifically, we calculated the difference between the change in the average value of an outcome before and after BM 110 in Oregon and the corresponding change in the synthetic Oregon.

Since large sample inferential methods are not appropriate when the number of units in the comparison group is small, we conducted permutation-based tests (Abadie, Diamond et al. 2010, Abadie, Diamond et al. 2015). Specifically, we first treated each of the 31 jurisdictions in the donor pool as the intervention state in lieu of Oregon, constructed the corresponding synthetic comparison, and calculated the difference-in-differences estimate to adjust for pre-policy time-invariant differences. If the estimate in Oregon is larger in magnitude relative to the estimates in these other jurisdictions, we considered that the estimate in Oregon was unlikely to have occurred by chance. The rank of the magnitude of the estimate in Oregon compared to the magnitude of the estimates in these other jurisdictions served as a permutation-based test p-value. Additionally, we reported the implied 95% confidence intervals from the permutation-based test p-value using the procedure outlined in Altman and Bland.(Altman and Bland 2011)

We conducted three sensitivity checks. First, we calculated an alternative p-value that takes into account the suboptimal fit in the pre-policy period (Abadie, Diamond et al. 2010). Specifically, after a synthetic control had been constructed for each of the control jurisdictions in the donor pool, we compared post- to pre-policy root mean squared prediction error (RMSPE) ratio in Oregon to the corresponding ratios in the control jurisdictions in the donor pool. The alternative p-value was then calculated as the proportion of post- to pre-policy RMSPE ratios in the donor pool that were at least as extreme as the ratio in Oregon. Second, we excluded neighboring jurisdictions from the donor pool to avoid potential spillover effects (Idaho, Nevada, and California). Third, we conducted “in-time placebo” following Abadie et al.(Abadie, Diamond et al. 2015) in which the policy effective date was assigned to the middle of pre-BM 110 period (July 2019). Fourth, we excluded the first 8 months since COVID-19 was declared as a pandemic by the World Health Organization (March, 2020 – October, 2020) from the study period to assess the potential influence of the pandemic on the estimated associations. Finally, to further avoid potential bias, we excluded states that have already legalized recreational cannabis prior to the study period from the donor pool.

RESULTS

Descriptive Statistics of Outcome Variables in Oregon without Adjustments

Drug-related fatal traffic crashes were around 0.25 per 100,000 population between January 2018 and January 2020 (Figure 1).2 There was a sharp increase to around 1 in the short period following the start of the Covid-19 pandemic, but it declined back by January 2021. The rate sharply increased again to around 1 in the few months following BM 110 and receded back afterward.3

Figure 1.

Figure 1.

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Comparison Before and After the Implementation of Oregon BM 110 between Oregon and Synthetic Control: Drug-related Fatal Traffic Crashes

Note. The vertical dashed line indicates when the Oregon BM 110 was implemented.

Identification of Synthetic Control

The weights used to construct the synthetic control for each outcome are reported in Supplementary Table S1, and the balance of the predictor variables between Oregon and its synthetic control is reported in Supplemental Table S2. Overall, the constructed synthetic Oregon overall approximated the sociodemographic characteristics and outcome trends in pre-BM 110 Oregon well.

The dashed line in Figure 1 shows the counterfactual estimates of what would have occurred in Oregon in the absence of BM 110. Overall, there is a lack of evidence that drug-related fatal traffic crashes would have substantially differed in the absence of BM 110.

Difference-in-differences Estimates

There is no evidence that BM 110 was associated with a change in drug-related fatal traffic crashes per 100,000 population (0.114, 95% CI: −0.106, 0.334) (Table 1).4

Table 1.

Difference-in-differences Estimates on the Associations between Oregon BM 110 and Drug-related Fatal Traffic Crashes

Average Pre-Post Difference: Oregon1 Average Pre-Post Difference: Synthetic Oregon2 Difference-in-Differences Estimates3 P-Value, P(|Δ Other| ≥ |Δ Oregon|)4 Implied 95% CI from the P-value5 P-Value Based on Post/Pre-Policy RMSPE Ratio6 Implied 95% CI from P-value (RMSPE Ratio)7
Lower Limit Upper Limit Lower Limit Upper Limit
Drug-related Fatal Traffic Crashes per 100,000 Population 0.240 0.126 0.114 0.313 −0.106 0.334 0.531 −0.235 0.464
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Note.

1)

Calculated as the change in the average value of the outcome before and after BM 110 in Oregon.

2)

Calculated as the change in the average value of the outcome before and after BM 110 in synthetic Oregon.

3)

Calculated as the difference between 1) and 2).

4)

Calculated using the distribution of the difference-in-differences estimates for the 31 control states in the donor pool. Specifically, the p-value of the two-sided test was calculated as the proportion of difference-in-differences estimates that were at least as extreme in absolute value as the estimate in Oregon.

5)

Calculated using the p-value in 4) based on the procedure outlined in Altman and Bland (2011).

6)

Calculated using the distribution of post- to pre-policy RMSPE ratios for the 31 control states in the donor pool. Specifically, the p-value was calculated as the proportion of RMSPE ratios that were at least as extreme as the RMSPE ratio in Oregon.

7)

Calculated using the p-value in 6) based on the procedure outlined in Altman and Bland (2011).

Sensitivity Checks

The alternative p-value reported in the 7th column of Table 1 supports the main finding. Excluding Oregon’s neighboring states from the donor pool yields qualitatively similar results (Supplemental Table S3). The “in-time placebo” analysis in which the policy effective date was assigned to the middle of pre-BM 110 period also shows no evidence of associations (Supplemental Table S4).5 Excluding the first 8 months since COVID-19 was declared as a pandemic from the study period also shows the robustness of the estimated associations (Supplemental Table S8).6 Finally, excluding states that have already legalized recreational cannabis prior to the study period from the donor pool yields qualitatively similar results (Supplemental Table S10).

DISCUSSION

This study did not find evidence that a policy that decriminalized non-commercial possession of virtually all scheduled drugs in Oregon, BM 110, led to an increase in drug-related fatal traffic crashes. This result is in line with the findings of previous works that found eliminating jail sentences for the possession of a small amount of a single illicit substance, cannabis, did not increase traffic fatalities (Aydelotte, Brown et al. 2017, Hansen, Miller et al. 2020). At the same time, however, it does not contradict the findings of previous studies that found traffic fatalities rose following a policy that eliminated the jail sentences for the possession of a small amount of cannabis either (Aydelotte, Mardock et al. 2019, Santaella-Tenorio, Wheeler-Martin et al. 2020). After all, our study only analyzed the short period following BM 110; it is possible that the impact of BM 110 could materialize in the longer run.

Our findings suggest that the concern of a rise in fatal traffic crashes following a policy that decriminalized virtually all illicit substances might be unwarranted, at least in the short term. We hope that our case study from Oregon’s BM 110 would be useful for policymakers who are weighing the benefits and costs of drug decriminalization policy in their effort to address the detrimental impacts of harsh drug sentencing guidelines.

This study is not without limitations. First, in addition to decriminalizing non-commercial possession of a controlled substance, BM 110 also establishes a drug addiction treatment and recovery programs which are partly funded by the state’s cannabis tax revenue and state prison savings. Although these programs were not fully funded until late 2022 (Russoniello, Vakharia et al. 2023), which is outside of our study period, part of the estimated associations might reflect the implementation of these programs. Second, although we utilized synthetic control method combined with difference-in-differences method, there might still be unobserved time-varying factors that confound the estimates. Therefore, our findings are best interpreted as associations rather than causality. Third, we were only able to examine the changes in outcomes up to 10 months following BM 110 due to data availability. It is possible that the impact of BM 110 could materialize in the longer term. As such, our findings are best interpreted as early evidence of the associations between BM 110 and drug-induced deaths as well as drug-related fatal traffic crashes. Fourth, the credibility of synthetic control method results relies on achieving a good pre-policy fit for the outcome of interest between the treatment unit and its synthetic control (Bouttell, Craig et al. 2018). Although this appears to be the case for the synthetic control used in this study, currently there is no consensus on what constitutes a good fit as well as how to judge similarity (Bouttell, Craig et al. 2018). Fifth, drug testing and reporting across states and time may not be uniform. Therefore, it may not be appropriate to make comparisons across states or time using FARS data. Sixth, FARS data are restricted to crashes that involve a death, and it is not possible to distinguish impairment from the presence of a drug. Finally, the presence of laws sanctioning driving under the influence of drugs in Oregon may diminish the impact of BM 110 on drug-related fatal traffic crashes. Therefore, the findings in Oregon may not be generalizable to other jurisdictions that implement drug decriminalization policies in the future.

CONCLUSION

BM 110 in Oregon reduced the penalty of a small amount, non-commercial possession of a controlled substance from a criminal misdemeanor to a new, Class E violation punishable by a maximum fine of $100. This study did not find evidence that the implementation of BM 110 was associated with changes in drug-related fatal traffic crashes. This finding suggests that the concern of a rise in fatal traffic crashes following a policy that decriminalized virtually all illicit substances might be unwarranted, at least in the short term.

Supplementary Material

1

What is already known on this topic:

  1. To date, the empirical evidence on the association between recreational cannabis legalization and fatal traffic crashes has been mixed.

  2. While the impacts of eliminating jail sentences for illicit substance possession on traffic fatalities has been explored before, previous studies have mainly focused on a single substance, cannabis.

What this study adds:

  1. We examined the changes in drug-related fatal traffic crashes following the decriminalization of virtually all drugs in Oregon (BM 110), the first state to adopt such policy in the United States.

  2. Policies that decriminalize virtually all illicit drugs may have a stronger impact on drug-related fatal traffic crashes than those that decriminalize only a specific substance.

  3. In this repeated cross-sectional study with a modified version of a synthetic control method, BM 110 was not associated with a change in drug-related fatal traffic crashes in Oregon.

How this study might affect research, practice or policy:

The findings suggest that the concern of a rise in fatal traffic crashes following a policy that decriminalized virtually all illicit substances might be unwarranted, at least in the short term

Funding/support:

This research was supported by grant #R01DA049730 from the U.S. National Institute on Drug Abuse (PI: Shi). This article is the sole responsibility of the authors and does not reflect the view of the National Institute on Drug Abuse.

Role of the Funder/Sponsor:

The funding organization had no role in the design and conduct of the study; collection, management, analysis, and interpretation of the data; preparation, review, or approval of the manuscript; and decision to submit the manuscript for publication.

Footnotes

Conflict of Interest Disclosure: Drs. Gunadi and Shi report no conflict of interest.

Research Ethics Approval (Human Participants): Not applicable. This study used publicly available secondary data.

1

It should be noted that the presence of laws sanctioning driving under the influence of drugs in Oregon may diminish the impact of BM 110 on drug-related fatal traffic crashes.

2

We chose January 2018 as the starting point for the analysis because it provides a sufficiently long pre-BM 110 period while also maintaining a sizable number of donor units in the construction of synthetic control.

3

For comparison purposes, we included Supplemental Figure S1 in which outcomes trends in Oregon were compared with the national trends.

4

There was also no evidence that BM 110 was associated with a change in total fatal traffic crashes per 100,000 population (0.155, 95% CI: −0.059, 0.368) (Supplemental Table S5).

5

We also tried other approaches such as interrupted time series and the conventional difference-in-differences (without synthetic control). The results for interrupted time series analysis are reported in Supplementary Table S6 and Figure S2. BM 110 was not associated with an immediate change as well as a slope change in drug-related fatal crash rate. The estimate from conventional difference-in-differences analysis indicates that BM 110 was associated with a 0.152 increase in drug-related fatal crashes per 100,000 population (Supplementary Table S7). However, the event study estimate suggests that the estimated association is likely to be driven by the difference in the pre-BM 110 trend (Supplementary Figure S3). It should also be noted that the cluster-robust standard errors used in the conventional difference-in-differences analysis can be too small when the number of treated clusters is small, leading to over-rejection of the null hypothesis (MacKinnon, J. G. and M. D. Webb (2018). “Pitfalls when Estimating Treatment Effects Using Clustered Data.”).

6

Using weeks as the unit of analysis yields qualitatively similar findings (Supplemental Table S9). It should be noted, however, that the synthetic control for the weekly-level analysis was constructed without including sociodemographic characteristics as predictors because CPS data are only available on a monthly basis

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Supplementary Materials

1
NIHMS2055627-supplement-1.pdf (583.5KB, pdf)

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