Deterrence, or Dissent? The Impact of Police Militarization on Protest Behavior
Abstract
Program 1033, which transfers surplus military equipment to local police departments, has faced scrutiny amid ongoing concerns over police brutality and the presence of militarized police at protests. Some scholars worry that such militarization has a “chilling effect,” deterring not just rioting but also peaceful protests, calling into question the constitutionality of militarization within the context of the freedom of assembly. Still others have found that militarization actually increases the frequency of protests, suggesting that police militarization is ineffective at deterring violent protests.
This study examines the impact of police militarization under Program 1033 on protest behavior, focusing on its role in deterring or inciting peaceful and violent protests. I use a time series panel regression on a state-by-state level from 2014 to 2023 to investigate this question. Even while accounting for lagged time effects and various social and economic variables, the data confirms that increased militarization has a statistically significant positive correlation with both peaceful and violent protests. This conclusion sheds light on the ineffectiveness of police militarization as it pertains to quelling violence, and it calls for policymakers to reassess the purpose and effectiveness of such policies on protecting communities.
1.0 Introduction
The American Traditions of Protest and Freedom of Speech
The United States stands on a foundation of rebellion and protest. From tossing tea into the Boston Harbor, to flooding the streets with crowds waving signs and harmonizing in chants, the freedom of speech as demonstrated through assembly has been a long-standing tradition. This form of free speech was recognized by the Supreme Court in 1937, and thus the right to assemble was codified into the Bill of Rights under the First Amendment (National Constitution Center n.d.).
Now, nearly a century later, the American tradition of protest stands strong. Movements against police brutality came to the political forefront with the killing of Michael Brown in Ferguson, 2014, and then to a boiling point in 2020 with the killing of George Floyd. Women assembled outside of the Supreme Court after the overturning of Roe v. Wade in 2022, and protests prevailed as the United States government funded a violent war in Palestine in 2023.
But just as protest movements have prevailed, so has the US government’s police presence within them. Instances of police violence and repression span decades, from ‘escalated force’ tactics in the 1960s to the use of tear gas and flash grenades by militarized police during the ‘Battle of Seattle’ in the 1990s (Vitale 2005). The smashes of batons have started sounding more like the pops of rubber bullets, and the “boys in blue” are now showing up in black, covered head-to-toe in riot gear and weapons of war.
This term, “weapons of war”, is meant in the most literal sense: through Department of Defense Program 1033, local law enforcement can acquire surplus military equipment ranging from lawnmowers and computers to tactical gear and armored vehicles. As police have become more visibly militarized, concerns around protest policing and violence have surged - especially as it pertains to the assembly clause. Are our police forces treading on the long-standing American tradition of protest? Is police militarization a threat to the First Amendment freedom of assembly? This study answers to what extent data can identify how the militarization of local police agencies through Program 1033 affects protest activity over time, opening the door for discussion about the policy’s effectiveness and militarization’s implications on the First Amendment right to freedom of assembly.
2.0 Background
Scholars present conflicting theories about how militarized police presence affects future protesters, by either deterring them through fear of violence, or inciting more protests due to antagonization. Although political parties debate the merits of police funding, training, and armament, both sides generally agree on the fundamental right to free speech and assembly.
2.1 Program 1033 and the Militarization of Police
Prior to the creation of Program 1033, the Defense Logistics Agency (DLA) was responsible for organizing the disposal of obsolete or excess military equipment, which was, at that time, either donated (like computers for schools), reutilized by other agencies, or demolished. In 1990, Congress authorized the excess equipment to be acquired by local law enforcement - first for the purpose of supporting the “War on Drugs”, and later to support counter-terrorism efforts. Thus, Program 1033 was introduced by the Law Enforcement Support Office (LESO) under the US Department of Defense (DoD) (Defense Logistics Agency (DLA) n.d.).
It wasn’t until 2014 in response to criticism of the Ferguson Police Department’s heavily armed retaliation against protesters that records were released about the transfer of equipment under Program 1033 to local law enforcement agencies. Program 1033 was criticized as enabling police to act more violently, and with a new light being shed on this program and pressure from the public for transparency, the Pentagon released military transfer data to the public in November 2014 [The Marshall Project (n.d.)].
In 2015, Obama issued order 13688, requiring improved oversight, protocols, and training, along with a ban on certain equipment being acquired - the list was small, but included highly militarized items like weaponized aircraft and grenade launchers, [Defense Logistics Agency (DLA) (n.d.)]. Then in 2017, Trump issued executive order 1368, which revoked order 13688 and also allowed bayonets and armored vehicles to be acquired once more, though some items - like grenade launchers - remained banned (Defense Logistics Agency (DLA) n.d.).
Support for the program cites its importance in crime-reduction, counter-drug, and counter terrorism efforts, including interference with mass shootings (Harris and Mills 2017). Critics cite concerns about police brutality and violence. The theoretical framework around militarization’s impact on protest behavior is vast, but quantitative studies between these two variables are limited. Scholars who have studied the impact of Program 1033 have often done so by measuring its effect on program-related goals, like crime rates. So, while literature studying the impact of Program 1033 or militarization in general does exist, most of it runs parallel to my study on protest behavior.
2.2 The “Chilling Effect” – A Deterrence Theory
The “chilling effect” is a legal concept introduced by the Supreme Court in the 50s that describes government actions that discourage individuals from exercising their First Amendment rights due to fear of retaliation or punishment. This term was introduced into the First Amendment in 1952, and has since been a commonly used term in legislative courts (Kendrick 2017); (Arnaud 2020).
Jamar Montgomery in Militarized Police and Unpermitted Protest: Implementing Policy That Civilizes the Police posits that police militarization discourages citizens from peaceful protest. “When demonstrators know that the police will show up with military weapons and hardware, they are less likely to exercise their constitutional right to freedom of speech and freedom of assembly because they are afraid of being dealt with harshly and violently,” [Montgomery (2016)].
Author Emmanuel Arnaud of Dismantling of Dissent: Militarization and the Right to Peaceably Assemble (2020) and author Ashley Eick of Forging Ahead from Ferguson: Re-Evaluating the Right to Assemble in the Face of Police Militarization (2018) also agree that police militarization has a chilling effect that, they conclude, undermines the First Amendment. Arnaud cites the violent dispersal of widely peaceful Occupy Wall Street protests in 2011 as a case study of problematic protest policing, raising questions as to why armed police were used to end the lawful assembly and whether or not this dispersal was unconstitutional [Arnaud (2020)]. Stating that Program 1033 brought “the types of materials used in wars…to our own backyard”, Arnaud illustrates the police violence that is enabled by this program and the threat it poses as having a chilling effect, deterring future protesters from peaceful assembly (2020).
Likewise, Eick posits that Program 1033 violates the Posse Comitatus Act, which prohibits the blending of military and police functions (Eick 2018). Using the 2014 Ferguson protests as a case study, Eick describes how an aggressive police presence escalated tensions and inflamed crowd behavior (Eick 2018). Eick argues that the intimidation tactics used by the police, including the visible use of tactical gear, military garb, and armored vehicles, serves as a deterrence to protesters and enables the police to exercise inappropriate levels of control over which protests are allowed or not (Eick 2018).
2.3 Militarization Leading to Escalation
While Eick cites the theoretical chilling effect that police intimidation can cause, she also reports on the DOJ’s investigation into the police tactics used in Ferguson. The DOJ reported on the role that militarization played in escalating the situation in Ferguson, citing that the use of tactical units can fuel more conflict towards the police as a result of heightened fear and animosity, and they called for a limited use of equipment such as armored vehicles, sniper rifles, and other tactical equipment (Eick 2018). Even in such a monumental case of violent protest policing, there is evidence that militarization failed to deter crowds and instead escalated protests into riots.
This opposing theory of escalation is cited in a number of case studies, but there are two empirical studies that expressly quantify to what extent protesters are either deterred or re-invigorated to attend protests in spite of increased police militarization. Authors of ‘I Will Be Out There Every Day Strong!’ Protest Policing and Future Activism Among Ferguson and Baltimore Protesters performed a study interviewing 102 respondents from Ferguson and Baltimore who engaged in street protests in response to the deaths of Michael Brown and Freddie Gray (Cobbina 2019). Their findings concluded that violent police tactics deterred “intermittent” and “tourist” protesters but failed to deter “revolutionary” protesters. Such people were characterized as deeply committed to the protest (Cobbina 2019).
While revolutionary protesters continued to return to future street protests, intermittent or tourist protesters who experienced violent protest policing were more likely to report being discouraged from returning to street protests, but instead expressed an intention to participate in advocacy in different ways (Cobbina 2019). While the previous interview-based study supports a mixed-theory conclusion, a study by authors Christos Mavridis, Orestis Troumpounis, and Maurizio Zanardi titled Protests and Police Militarization, found that increased police militarization overall incites more protest activity, (Mavridis, Baker, and Smith 2022). Mavridis and team state that, by using empirical literature regarding Program 1033 in combination with ACLED protest data, they were able to obtain statistically significant causal estimates of the effect of militarization on total protest activity: “In a nutshell, we find that militarization increases the incidence and number of protests in a county” (Mavridis, Baker, and Smith 2022).
2.4 Parallel Research
Although many scholars write extensively about political theory, law, and the constitutionality of protest repression, there are limited empirical studies that examine militarization’s causal effect specifically on protest behavior. Instead, many such studies measure its effect on variables like crime rate, police violence, or public perception.
For example, authors Vanessa Willaimson, Kris-Stella Trump, and Katherine Einstein in Black Lives Matter: Evidence That Police-Caused Deaths Predict Protest Activity”, [Williamson, Trump, and Einstein (2018)] performed an empirical study between police-caused Black deaths and protest activity - their findings concluded that such police killings do predict protest activity. Other studies, like Peacekeeping Force: Effects of Providing Tactical Equipment to Local Law Enforcement by Matthew Harris through the American Economic Association (AEA) [Harris and Mills (2017)] studied the relationship between militarization through Program 1033 and crime rate. They did not research its effects on riots or protests, nor did they examine a multi-year period (just 2014) (Harris and Mills 2017). Rather, they measured its impact on curbing crime rates, which they stated to be positive.
Other studies, such as (Gunderson et al. 2020) have expanded upon this study by the AEA, finding flaws in its methodology. Upon accounting for geographical effects, Gunderson and team actually disproved the AEA’s claims about Program 1033, demonstrating that it had no statistically significant effect on crime rate. While neither study looked at protest behavior, the designs of both studies inform my methodology, as they also use militarization data about Program 1033 as their independent variable.
3.0 Theoretical Development
Informing Study Design and Hypothesis Using Existing Literature
The aim of my study is to determine to what extent data is able to prove or disprove the idea that police militarization has a chilling effect on future protests. Understanding the theoretical and empirical studies on police militarization’s effect on protest behavior serves as an informative foundation upon which my study is designed. Taking into account theories and designs of existing studies, I designed my research intentionally to expand upon this pool in order to expressly address militarization trends of police departments over time across the United States, and measure whether or not this has a statistically significant impact on protest behavior.
3.1 Hypothesis
I began this study with the prediction that the data would show increased militarization through Program 1033 deters violent protests. Further, I predicted that after this initial chilling effect in response to immediate police violence, lagged data would show an increase in protests due to retaliation.
3.2 Theoretical Development
In my background section, I briefly discussed two studies that measure the causal impact of police militarization on protest behavior. I’ve chosen to model some of my research off of the study by Mavridis and team, as this studies the same topic as mine but with a handful of differences.
Mavridis’s team looked only at year 2020, and they used LESO data from 2019 to observe a lagged effect on protest quantity. They used data from ACLED as opposed to my study which uses protest data from GDELT. I will describe these elements in detail in section 4.1. Further, they use LESO data in consideration with all previously acquired equipment, which is not accounted for in my study, as LESO only provides transferred equipment, not currently-held equipment. They broke their militarization data down by types of equipment (including total). Finally, they look at county-level as opposed to state-level.
Their findings show that violent protests are not affected to a statistically significant degree by any type or total equipment acquired. Further, they looked at protest topics and found that militarization has a positive and statistically significant impact on BLM protests, but no impact on COVID protests. Finally, their overall findings are that increased militarization increases the incidence and number of protests overall (no effect on violent protests). They control for median household income, population, Black population percentage, percentage of Trump voters, and HIDTA-classified counties (High Intensity Drug Trafficking Area). I too included median household income, population, and Black population percentage, but also added a variety of other socioeconomic control variables.
3.3 Expanding on Existing Literature
In this study, I expand upon the limited existing empirical research between militarization and protests to identify how the nature of protests have changed from 2014 to 2023 in response to police militarization through Program 1033, both in quantity and type of protest. I’d like to challenge the existing conflicting conclusions in the literature and use my collection of data to confirm or reject existing hypotheses, ultimately determining if militarization is a deterrent to freedom of assembly.
I’ve chosen to also measure the impact of militarization separately on peaceful, violent, and total protests. Observing how militarization impacts different types of protests will shed light on whether legislation like Program 1033 1) are successful at deterring violent protests or riots, 2) unsuccessful at deterring violent protests or riots, 3) fail to deter and instead incite more protests or riots, or 4) if they are overly successful and not only deter violent protests but also peaceful ones. Mavridis’ study also examined the impact on total protests and violent protests, from which implications about peaceful protests can also be made. This and my own research sheds light on what non-empirical case studies haven’t as explicitly answered.
Mavridis’ study is limited in that it only looks at the lagged effect of 2019 militarization on 2020 protests. This study builds on existing research by analyzing 10 years of data from 2014 to 2023. This not only covers an essential protest period during the Ferguson protests of 2014, but it also covers the unique COVID and post-COVID landscape of 2020 - 2023. This additional data will be essential in telling a more robust story of how militarization impacts protests and whether or not these trends hold up to the test of time.
Mavridis and team uses ACLED protest data, which is a limiting factor in that it only provides data from 2020 onward. For this reason, I chose to use the GDELT dataset, which spans from 2013 onward. Using this dataset allowed me to study a longer timeframe but also introduces a different element to my study and contributes a unique element to the existing body of research.
Information discovered from my study should guide discussions on the constitutionality of excessive police militarization and its impact on the First Amendment’s freedom of assembly. In an age where freedom of speech is regularly a hot topic, the other freedoms to expression listed in this amendment should not be forgotten.
4.0 Data and Methods
A Deep-Dive Into Datasets, Design, and Statistical Considerations
4.1 Explanation of Data Sources
To examine the relationship between police militarization and protest behavior, I’ve run a time series panel by year and by state in the United States from 2014 to 2023. Protest event data is available from the Global Database of Events, Language, and Tone (GDELT Project n.d.). This database provides details of demonstration events pulled from news articles, including location, time, purpose, and type of demonstration from 2013 to 2024. Demonstrations are defined as “Dissent collectively, publicly show negative feelings or opinions; rally, gather to protest a policy, action, or actor(s),” (GDELT Project n.d.). Other forms of demonstrations that are tracked include hunger strikes, strikes or boycotts, obstruction of passage (defined as “Protest by blocking entry and/or exit into building or area,” (GDELT Project n.d.)), and violent protests or riots (defined as “Protest forcefully, in a potentially destructive manner,” (GDELT Project n.d.)).
I chose to only include “demonstrations”, “obstruction of passage”, and “violent protests or riots” in my analysis as my dependent variable, as they are relevant to the First Amendment freedom of assembly. Given that this is defined in the US constitution as “the right of people to peacefully gather and express their ideas”, I am excluding hunger strikes (defined as “Protest by refusing to eat until certain demands are met,” (GDELT Project n.d.)) and boycotts (defined as “Protest by refusing to work or cooperate until certain demands are met,” (GDELT Project n.d.)). These two activities are not characterized as gatherings, but are generally passive acts of restraint where police involvement is not relevant. For this reason, I am not including these types of demonstrations reported in GDELT in my analysis. I am also excluding events labeled with “All civilian demonstrations and other collective actions carried out as protests against the target actor not otherwise specified,” (GDELT Project n.d.), due to the ambiguity of this classification and also the fact that peaceful and violent protests are already accounted for in the other categorizations.
GDELT provides protest data from 2013 to 2024, but I chose to only look at 2014 - 2023. I excluded 2024 as this study is currently being conducted in this year, so there is not a year’s worth of data available. I also chose to exclude 2013 because it only listed 9 protests occurring compared to the following years which ranged from 1,006 (minimum) to 139,379 (maximum), indicating that data for 2013 is missing from GDELT or more broadly categorized, disqualifying events from being included in this study. I chose to leave 2014 in (this had 1,006 protests, whereas the next lowest protest year was 2022 with 45,508 protests) because whether I included it or excluded it, my conclusions were not changed - coefficients and statistical significance remained virtually unaffected. I also took the log for this variable to account for highly-skewed data across states, which also helps to accommodate 2014 as an outlier. My model fit was better when including 2014, which is why I chose to keep it instead of removing it. I also accounted for concerns of possible missing data using clustered standard errors.
I am measuring police militarization using data from the US Defense Logistics Agency, specifically the Law Enforcement Support Office “Property Transferred to Participating Agencies” dataset, which details a record of military property that was shipped to local police departments through Program 1033. Shipment data includes a list of property, the value of the property, the quantity of items, and their ship date per police agency in each state. Data dates from 1998 to 2024.
I will be measuring “militarization” by the acquisition value (USD amount) of property acquired per state over time. This is the value of the equipment that the law agency acquired, as these items were not purchased by the local agencies. The acquisition value will be my independent variable in this study. Property included in the Defense Logistics Agency (DLA) dataset ranges from lawnmowers and computers to pistols and armored vehicles. Clearly, the range of product types is vast, and not all products are indicative of militarization or armament. For the purpose of this study, I used LESO’s demolition codes to determine which items should be excluded from this study for not being associated with militarization.
Concerns with using LESO’s dataset of 1033 Program equipment transfers have been published by Koslisky (Koslicki 2022), with one primary concern being that many studies that use this dataset fail to recognize that items coded with demilitarization code “A” (DEMIL A) are only included in datasets as a “snapshot in time”, meaning that, quarterly data only shows DEMIL A equipment that was acquired that quarter, and does not maintain any historical context of how much equipment the agency has maintained or returned. So, analysis surrounding these items varies by study and is not accurate. LESO defines DEMIL A items as “determined by the DoD to present a low risk when released out of DoD control. No DEMIL, MUT, or end use certificate is required” (Defense Logistics Agency (DLA) n.d.). For context, DEMIL A items include digital cameras, survival blankets, boots, and other similar items.
In my study, I elected to exclude DEMIL A equipment from my “militarization” variable, as I only wanted to focus on items that can reasonably be perceived as intimidating (vehicles at protests) or can reasonably be used during protests (protective goggles). Since DEMIL A equipment does not require demolition and generally includes typical administrative supplies, I consider this code to be a good indicator to allow me to remove items without introducing human bias of what is and isn’t militarized or intimidating. I believe it is necessary to exclude such items, as the lens through which I am looking at police militarization is the physical or perceived harm it causes on the community, resulting in either deterrence or more unrest. A list of the equipment, along with the demolition codes, can be found on the LESO website.
4.2 Summary of Statistics and Content Overview
Below I present a summary of the statistics from GDELT and LESO, aggregated by state and year. Figure 1 shows statistics for GDELT protest data, which should be interpreted like so: the average number of protests one state had in any given year was 1,224.
The second section in Figure 1 summarizes demographic metrics again by state-year combo gathered from the US Census and other sources, cited below.1 The final table summarizes LESO data and can be interpreted like so: the average sum value of total military equipment any one state acquired in a given year was $28 million. Note that the state of Virginia had no military equipment acquisitions in 2023; they acquired only class “A” items, which were excluded from my model. I created a placeholder value of $1 for Virginia, 2023, which is reflected in the summary statistics table (Figure 1) as the minimum spender.
Including VA in the model reduced the coefficients on total protests by 0.08 points and reduced the statistical significance of poverty rate from 0.001 to 0.05 for peaceful/total protests. The Adjusted R^2^ values and F statistic both decreased but to a very small degree. A model that excludes VA is in the appendix to show the results excluding this outlier (Figure 4). However, I believe it is important to keep this outlier in my main model as it is an example of a state that had almost no militarization growth but still had protests.
Figure 1: Summary of statistics used in the primary model
4.3 Methodology
I created a time series panel model of my variables to assess if there is any statistically significant correlation between increased militarization and number or type of protests. I used a panel log model (plm) to regress militarization (independent variable) and protest count (dependent variable) per state (units) across time. I used data spanning from 2014 to 2023 and applied years as fixed effects. To account for the variability of the militarization and protest variables, I used their log values and included robust standard errors in my final model.
The model also contains socioeconomic control variables including population, crime rates, race, gender, age, partisanship, unemployment rate, poverty rate, and military GDP in order to isolate the impact of police militarization.2
I included lagged time effects to my model to observe if militarization has a delayed impact on protest behavior and, I conducted a variety of validation and robustness checks to ensure that the statistical significance and coefficients are reflected accurately.
5.0 Statistical Results and Findings
Below, I present the statistical results of my study, first detailing a summary of overall conclusions, and then diving into specific variations and robustness considerations.
Figure 2: primary model showing police militarization impact on protest with fixed time effects and lagged protests
5.1 Overview of Main Findings
This model, shown in figure 2, concludes that there is a positive and statistically significant correlation between police militarization and protests, both peaceful and violent. The effects are statistically significant at the 0.01 level and persist across models with various controls and fixed time effects. Police militarization has an immediate (within the same year) effect on each type of protest, it has a lagged effect (lagged by 1 year) on only violent protests.
Poverty rate and military GDP also show statistically significant impacts: lower poverty rates correlate with increased protests, while higher military GDP is linked to more peaceful and total protests. Lastly, population size is also statistically significant, but at the 0.1 level for peaceful and total protests, and suggests that as population decreases, protests increase.
In all, this model includes 480 observations (48 states and 10 years, where Hawaii and Vermont are not included due to having no LESO data. Neither Hawaii nor Vermont participate in Program 1033 (LESO, 2024)). I held a variety of variables constant to take into account the different factors that could impact protest behavior. This included state population size, median age, percent of Black population, percent of Hispanic or Latino population, ratio of democrat to republican house representatives (partisanship), crime rate per 100k people, and poverty rate. In addition, I held year effects constant to isolate their influence. This is particularly relevant for this project since between 2014 and 2023, we experienced two presidential elections, a pandemic, and multiple large political movements (BLM, Women’s March), that could affect protest behavior regardless of other factors.
To account for variability in my independent and dependent variables, I used the log value of militarization and protest data. This makes interpreting the coefficients less intuitive, but we can observe their relative impact to one another. For example, increased militarization predicts more peaceful protests than violent protests. For every 10% increase in military acquisitions in dollars, there is a 4.29% increase in peaceful protests, and a 1.96% increase in violent protests. We can also see through the coefficients that lagged militarization has a greater effect in the immediate term than in the long-term, with predicted violent protests decreasing from 1.96% increase to a 0.56% increase with every 10% increase in military acquisition value, (Figure 2).
5.2 Time Series and Lag Considerations
Before holding years constant, lagged protests, partisanship, unemployment rate, and poverty rate were statistically significant at the 0.001 level. Militarization remained statistically significant but with slightly lower coefficients across the board (Figure 5). This suggests that, in addition to militarization, partisanship, poverty, and unemployment can predict which states are more likely to protest. The significance of lagged protests also supports the idea that time-effects are essential in explaining this model. These things are interesting to keep in mind once we add in years as fixed effects, because the temporal aspect fills in the model fit more significantly (increasing Adjusted R^1^ from 0.612 to 0.888 for total protests) while also removing any statistical significance from those variables, with the exception of poverty rate.
Figure 5: model without fixed time effects - before holding years constant
Time-related events, whether political events, laws, or media and social influence, account for a significant impact on protest behavior, removing any statistical significance from partisanship, poverty, or unemployment once accounted for. We are left with a well-fit model that still proves that militarization has a significant impact on protest behavior. We can see in the final model, Figure 2, that all years across all models are statistically significant to at least the 0.05 level if not the 0.01 level, and that the coefficients generally decrease over time with post-COVID years (2021 - 2023) predicting fewer protests.
5.4 Univariate Analysis
As a reference, in Figure 9, I illustrate the number of events over time, and the figure shows visually the decrease in activity in post-COVID years.
Figure 9: protest count year over year (GDELT Project n.d.)
Figures 10 and 11 help to visualize outlying states in regards to total protest count by state (total for all years) and total acquisition cost by state (total for all years). Below, we can see that California and New York stand out as having the most protest over time, while Texas and California have the highest aggregate acquisition value. The heatmaps in figures 12 and 13 illustrate how these variables changed over time, allowing us to observe any outlying years that skew aggregate data. For example, Texas in 2014 acquired 54 of mine resistant vehicles, nearly all of which had an acquisition value of $733,000. This exemplifies the importance of using fixed time effects in this study, as well as using logged values for the dependent and independent variables, to best understand the relationships over time.
Figure 10: total number of protests per state from 2014 - 2023 (Defense Logistics Agency (DLA) n.d.)
# A tibble: 0 × 9
# ℹ 9 variables: State <chr>, Item_Name <chr>, Quantity <dbl>,
# Acquisition_Value <dbl>, DEMIL_Code <chr>, DEMIL_IC <chr>, Date <dttm>,
# Total_Cost <dbl>, Year <dbl># A tibble: 1 × 9
State Item_Name Quantity Acquisition_Value DEMIL_Code DEMIL_IC
<chr> <chr> <dbl> <dbl> <chr> <chr>
1 VA DUMMY ROW 1 1 Z N/A
# ℹ 3 more variables: Date <dttm>, Total_Cost <dbl>, Year <dbl>Figure 11: total acquisition value per state from 2014 - 2023 (Defense Logistics Agency (DLA) n.d.)
Figure 12: count of protest occurrences over time by state (Defense Logistics Agency (DLA) n.d.)
Figure 13: militarization over time by state and year (GDELT Project n.d.)
Figure 13 demonstrates that military equipment acquisition was at its height in 2014 and new material acquisition dwindled over time. Figure 12 identifies California and New York as protest hotspots, while also illustrating that years 2016 and 2020 were highest in protest activity.
I included charts of my independent and dependent variables to visualize the need for normalization, and also to simply illustrate how states and years differ per variable, hopefully inspiring conversation or future research into the specific events or locations that serve as anomalies.
Items acquired through Program 1033 range significantly in value, from a $2 million dollar aircraft acquired by California in 2016, to a one-cent radio-set sent to Virginia in 2016. Taking the log of the militarization variable helps to account for outliers, but I also wanted to visually confirm that the quantity of items acquired falls in line with the total value. Below is a look at total spent on military equipment in the US per year. To summarize the findings in Figures 14 and 15, we can again see which years and states stand out for having the largest acquisition values. 2014 and 2016 were big years for acquisition through the 1033 program. The average value per item generally aligns with the spikes in spend, and for the most part, so does the quantity of items acquired, except for in 2018, where many low-cost items were acquired, as seen in the quantity spike in Figure 14 and the value dip in Figure 15.
Figure 14: acquisitions quantity and value (Defense Logistics Agency (DLA) n.d.)
Figure 15: acquisition cost and value (Defense Logistics Agency (DLA) n.d.)
As seen in Figure 15, it appears that spikes in acquisition value totals correlate with spikes in average item value, suggesting that years with higher spending were also impacted by the acquisition of higher-value items. Investigating the impact of different categories of items on protest behavior would be an interesting topic to dive into - similar to Mavridis’ team’s study.
5.5 Data Validation
To ensure my model accurately represents true effects, I ran some validation tests and included robust standard errors. The robust standard errors, shown in parenthesis to the right of the coefficients in each regression model, demonstrate the precision of the effect of militarization on protest behavior, with good precision being attributed to those where SEs are much smaller than their coefficients.
Using this robust model also takes care of heteroskedasticity and serial correlation that I identified in my model. In a plot of residuals versus fitted values, I visualize the randomness of residuals and any concern for outliers or heteroskedasticity. Figure 15 shows that the splay of residuals is generally random and centered around 0, but a slight clustering towards the right of the plot suggests that heteroskedasticity may be present.
Figure 15: residuals plotted against fitted values for militarization’s impact on protests (GDELT Project n.d.); (Defense Logistics Agency (DLA) n.d.)
To measure this, I ran a White Test and confirmed that heteroskedasticity does exist. Models with log-transformed variables often experience heteroskedasticity due to the compression of larger values. It is important to note that the White Test works best for linear or quadratic models, and my model is a panel log model. However, the White Test does still indicate heteroskedasticity in this case - which can be accounted for using clustered standard errors, which I included in my model.
I also performed a Breusch-Godfrey (BG Test in R) and Breusch-Godfrey/Wooldridge (PBG Test in R) to test for serial correlation. The result suggested that there is evidence of some serial correlation, which could be caused by temporal or spatial dependence across my model’s observations. Robust (clustered) standard errors can account for this, too, so this has been addressed in my model. I suspect that, considering the moderate VIF collinearity values on my years values, that the serial correlation culprit is a temporal dependence. This could be an area for future researchers to investigate further.
Overall, after including robust standard errors, the direction of my coefficients and level of significance for p-values remains the same. With a statistically significant F Statistic at the 0.01 level, and with Adjusted R^2^ values of 87.9%, 71.1%, and 87.8% for peaceful, violent, and total protests respectively, and also with consideration to the variations of my model as demonstrated without fixed time effects, and with different control variables, one may conclude that the model is well-fitted considering the complications that come with time series and panel models.
6.0 Conclusion
As seen in my final regression model in Figure 2, an increase in police militarization as measured by an increase in acquisition value of military equipment through Program 1033 has a positive and statistically significant correlation with an increase in all protests, regardless of type. The effect is higher on peaceful protests compared to violent protests. We can conclude that militarization 1) does not have either an immediate or a lagged chilling effect on protest behavior, 2) is not successful at reducing violent protests, and 3) does predict an increase in same-year protests, along with 1-year lagged violent protests.
While this disproves a portion of my initial hypothesis, it does confirm other studies like Madrivis et al.’s that observe that protest behavior increases in spite of police militarization, with the main difference being that my study shows an effect not just on peaceful but also on violent protests, unlike Madrivis et al.’s study.
While this shifts the discussion away from militarization’s impact on suppressing the First Amendment freedom of assembly, it instead shifts the focus on the effectiveness of police militarization at all. Given the recent rise in protests against police brutality, it is unsurprising that increased militarization fuels further incidents of brutality or reinforces negative perceptions of police, prompting additional protests.
6.1 Policy Implications
Program 1033 fails to reduce violent protest activity and instead incites more protests, both immediately and over time. Additionally, research found that Program 1033 has no effect on crime rates, which was its initial purpose (Gunderson et al. 2020). My own study, while not designed to measure the effect on crime rate, does control for this variable and also finds there is no statistical significance. These findings call into question the purpose of maintaining Program 1033 if what it effectively does to a community is incite more protests and riots.
The connection between police militarization, the negative public perception it’s garnered, and evidenced escalation of violence in protests, has sparked discussion around police reform with ideas like improved training, “defunding”, reallocating budget to constructive or preventative resources, or completely reinventing the system. With data supporting the consensus that militarized police do not quell violent protests, policy makers should begin taking these public criticisms seriously.
Militarized police and protest policing has been criticized for its potential to deter future social movements, threatening freedom of assembly, but my findings here suggest a need for policy makers and scholars alike to recognize the antagonizing force that militarization brings.
6.2 Ideas for Future Studies
In future studies, it would be worth examining other legislation that has enabled police militarization, such as Program 1122, which “allows local police entities to purchase new military equipment using their own funding with the same discounts received by the federal government.” [Police Foundation (n.d.)].
Choices in how to categorize military equipment from LESO records certainly has an impact on how militarization is measured, so this could also be something to consider testing different definitions of. Like the study from Mavridis’ team, categorizing different types of military equipment to observe their impact on protest behavior would also be worth exploring, [Mavridis, Baker, and Smith (2022)].
Testing this model with other protest datasets, like ACLED or Crowd Counter Consortium, would also be worth testing. While I selected GDELT for its longer timespan, the method of data collection used for GDELT (machine learning algorithms identifying and categorizing protests and other events by crawling news articles) calls into question its accuracy. However, considering that my findings are not too dissimilar from Mavridis’ team’s findings using ACLED, I do feel confident that GDELT is an adequate choice.
Investigating the impact on crowd turnout would also be worth studying - this data is available through Crowd Counter Consortium, but only from 2017 onward, hence my choice to exclude it as a variable in this study.
Finally, accounting for state (spatial) fixed effects in order to observe the effects of possible spillover into neighboring states may help to improve the model fit even more. Future researchers could also consider using county-level data from GDELT as opposed to state-level data for even clearer data.
Appendix
Figure 3: summary of data
Figure 4: a variation on the primary model, this time excluding Virginia
Figure 6: a separate model that demonstrates the impact of gender, age, and GDP variables by replacing median age and female percent with males over 18, and replacing military GDP with government GDP
Figure 7: the collinearity of all variables
Figure 8: a variation on the primary model that includes observed lagged cost (+1 year lag)
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Footnotes
Militarization data as acquisition value through LESO, [@DLA]. Protest count, type, and population, [@GDELT]. Age, gender, and race data, [@USCensus2024]. Democrat and Republican ratio, (NCLS, 2024). Military GDP and government GDP, [@BEA2024]. Police-caused deaths, [@MappingPoliceViolence]. Crime rate, [@FBI]. Unemployment rate, poverty rate, [@Walker2024].↩︎
Military GDP is defined by the Bureau of Economic Analysis as “The estimates of wages and salaries for the military services consist of cash wages (including allowances) of full-time personnel of the armed services (including the Coast Guard), cash wages of the members of the Reserves including the National Guard, and pay-in-kind received by the full-time and reserve enlisted personnel of the armed services” (U.S. Bureau of Economic Analysis (BEA) n.d.).↩︎