Harm reduction approaches to manage the risks or consequences from opioid use have already helped reduce rates of infectious disease transmission from injection drug use and overdose deaths. They have also helped reduce the stigma associated with drug use, which is a major barrier to treatment and care. These are excellent developments. However, whenever the consequences of risky behavior are diminished (even when they are purposefully reduced to achieve a
net-benefit), there is a chance that the risky behavior may escalate. This is
known by economists as a “moral hazard.” For example, during bad weather,
drivers with All Wheel Drive (AWD) often take more risks than drivers without
the feature. This is likely because drivers with AWD believe they are protected
from the increased risk of driving in snow, so they may not adjust their
behavior to account for the adverse conditions.

With respect
to harm reduction, a recent study by Jennifer L. Doleac and Anita Mukherjee
argues that expanded naloxone access increases opioid abuse and crime, while
having no effect on overdose mortality. Such increases, they argue, occur
because naloxone prolongs the lives of people who use opioids (allowing them to
continue drug use) and increases the likelihood that people may use in a more
risky manner, simply because naloxone is available if they overdose.
Furthermore, because naloxone may increase the number of people who use
opioids, theft and other crime may increase to support use.

While such arguments
may seem plausible, albeit distasteful, they are simply contradictory to the
existing body of research on the expansion of naloxone access. And, while it is
true that sometimes evidence emerges that successfully disproves years of
previous research, this is not one of those cases, as the study’s conclusions
are based on questionable methods, a narrow dataset and far too many
questionable  assumptions.  

With respect
to the study’s methodological problems, a primary one is that each of the
associations presented in the paper are derived from many, diverse data sources
that were not designed to be combined. For example, data is derived from (among
others) Google search trends, The
National Incident-Based Reporting System
, The
Healthcare Cost and Utilization Project
, a restricted-use dataset on opioid overdose
mortality from the Centers for Disease Control and manually collected data on
state-level naloxone access laws.

datasets is problematic because each of their data collection methods may differ
significantly. In this case, it is of particular concern because the authors of
the study failed to describe how the large number of datasets compared
methodologically, and (worse yet) they provide no description of the methods
used when collecting the data they personally contributed to the study.
Additionally, many of the associations they derived were from proxy variables
intended to represent a different exposure than the variable measured.
Essentially these types of substitutions create a scenario similar to replacing
a key ingredient in a recipe; the result may be good or bad, but it’s definitely
not the same as the original. In this case, their choices of proxies are often
not ideal and the choice to restrict their analysis to urban areas with
populations greater than 40,000 make it difficult to generalize the findings to
other areas of the United States.

The study’s
findings are also plagued by its empirical strategy. For example, to determine
how expanded naloxone access impacts behavior, the authors compared
jurisdictions that adopted naloxone access laws against those that did not. In
so doing, they used a differences-in-differences (DD) model, commonly used in
program evaluation to evaluate outcomes resulting from an intervention. Such a
model requires the use of longitudinal data (data collected from the same
subjects at multiple time points over a set period), and relies on several
assumptions, most importantly, that in the absence of treatment, the difference
between the treatment (areas with expanded naloxone access) and control (areas
that do not have expanded naloxone access) groups remain constant over time.
This is known as the “parallel trends assumption.”

However, since
opioid overdose mortality rates were not increasing uniformly across
jurisdictions during the study period, it’s unlikely this assumption was valid
and likely that it led to inaccurate results. This is because the parallel
trends assumption is the most important assumption made in the DD model. Therefore,
if the assumption is not valid for the data, the resulting estimate will be
biased and in some cases, extremely so. Since it is likely that naloxone
expansion is happening in response to rapidly increasing overdose deaths or the
increasing prevalence of opioid use, the intervention group is very likely changing
at a more rapid pace than the control
group. Unfortunately, to date, research to confirm or refute this hypothesis is
lacking and although the authors attempt to address this concern, it is unlikely
that their model adjustments sufficiently control for the differences between
treatment and control groups.

concern is that the authors fail to correct for autocorrelation across time
periods. Put simply, this is when the value of an observation in a time series
is influenced by the value of a previous observation. Such a failure to correct
can result in erroneous
conclusions up to 85 percent of the time
, as it biases
the estimate at each subsequent time point and results in the erroneous conclusion
that there is an association between variables. Doleac and Mukherjee suggest
that the results of their analysis are robust, and provide several analyses in support.
However, without evaluating the impact of autocorrelation, there is no way to
determine the validity of the results.

Finally, the
follow-up period after the implementation of naloxone access law was no more
than 12 months for any measure and, in some cases, was only six. It is
questionable if such short follow-up can accurately reflect the impact of the
law. After all, there is no such thing as perfect implementation or information
in public health, and often those most in need of intervention access do not
learn about available programs until long after original implementation.

All of this
is to say that while, on the surface, Doleac and Mukherjee present a fairly
convincing argument that naloxone access laws may not have the desired effects,
their results depend on so many assumptions that it is difficult to trust their

Perhaps more
disturbing, however, than the questionable findings themselves are the
potentially dangerous takeaways that may be extrapolated from them. We should
never condemn a policy that provides access to a lifesaving treatment based only
on the possibility of negative externalities like property crime. Even if,
under the many assumptions of this model, the overdose mortality rate remained
stable, no one can argue against the fact that naloxone saves individual lives.
And accordingly, increased availability may be very literally be the difference
between life and death.

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