Recruitment.

Participants were recruited from areas of Baltimore identified as areas of high drug-related activity (see Aim 2 methods for more detail). Study staff drove a mobile van to these locations and informed women appearing to be 18 years or older about the study opportunity. Interested individuals returned to the mobile van for eligibility screening and, if eligible, provided oral informed consent. Recruitment used purposive sampling to capture a broad range of experiences in terms of demographics (e.g., race/ethnicity, age); behaviors (e.g., drug types used, length of drug use); and social context (e.g., experiencing homelessness, strength of social ties). Inclusion criteria for Aims 1 and 2 were: ≥ 18 years; self-identify as a woman; and used opioids (e.g., heroin, pills, fentanyl), crack cocaine, and/or cocaine more than 3 times in the past 3 months.

In-depth interviews with WWUD.

Interviews were conducted using a semi-structured guide that explored a range of topics related to peer recruitment methods, including Respondent Driven Sampling (RDS), to examine the appropriateness of using a modified RDS method. Interview questions addressed women’s peer networks, attitudes towards peer referrals within those networks, concerns and strategies to mitigate them, and logistical considerations for recruitment (e.g., incentive type and amount, ways to retain coupons). Participants were compensated with a $50 Visa gift card per interview. Audio recordings of the interviews were transcribed verbatim for data analysis.

This study marked our first use of modified-Respondent-Driven Sampling (RDS) for recruiting within this population, despite our long-standing engagement and prior research with them [11–15,19,31–33]. We originally planned for N = 20 interviews, but reached saturation after N = 12 interviews; therefore, we stopped data collection as no new insights emerged from additional interviews.

Data analysis.

Qualitative data management and analysis were conducted using MAXQDA software. All interview recordings were transcribed, translated where necessary, and uploaded to MAXQDA for coding and analysis. Data analysis followed these successive steps: 1) multiple readings of transcripts with memoing to note initial key themes; 2) open coding of selected rich passages; 3) coding of all interviews; 4) grouping, comparison, and categorization of themes by interview; 5) synthesizing and comparing through thematic analysis [34].

Sample size calculation.

For sample size calculations, power analyses assumed up to 25% loss to follow-up and an average of three follow-up visits per participant over 18 months. For the non-fatal overdose outcome, assuming a cumulative rate of 36% in the control group and lower rates in the intervention group, the study has 85% power to detect RR = 0.56 (or 80% power for RR = 0.58) with N = 400. With N = 300, the detectable RR is 0.50 at 85% power. These estimates suggest that the proposed sample size provides adequate power to detect clinically meaningful effects under realistic follow-up conditions.

Geographic zones.

We are recruiting N = 250 WWUD in the two existing geographic zones where Mobile SPARC currently operates in West Baltimore. Mobile SPARC staff mapped their existing outreach route using the Strava app to determine geographic service boundaries and, consequently, the study’s data collection boundaries. N = 150 WWUD are being recruited in ‘control’ areas. Control zones were identified based on high concentrations of 911 calls for overdose and drug arrests from the Baltimore Fire and Police Departments using a publicly available municipal database. These geographic areas in Northwest and East Baltimore are comparable in terms of population and drug activity. However, the control areas lack routine exposure to SPARC and its mobile outreach catchment services, and recent research also indicated that WWUD in these areas rarely report utilizing SPARC’s services [35]. The control areas are served by other health and social services for vulnerable populations. One harm reduction-focused organization serves people who use drugs with mobile outreach services, though our control areas are outside of this organization’s typical catchment area.

In each geographic zone, we first conduct a windshield and walkthrough tour of the recruitment site in pairs of two or three. These tours help validate the appropriateness of zones that were identified using 911 and arrest data. Study staff have forms on which to note how many people in the area appear to be women over 18 years old, pedestrian traffic levels, businesses nearby, and locations to park the RV for recruitment. Based on these observations, the team determines whether the zone is appropriate and identifies an optimal RV parking location.

Modified RDS method and network analysis.

Recruitment into intervention and control groups utilizes a modified RDS method. RDS is a non-probability chain referral sampling method that has been widely used to engage populations that lack a sampling frame [36]. The method, including modified versions, has been used in research conducted in Baltimore City [37,38]. Because this method leverages trust and connections within communities, it was refined for use in the National HIV Behavioral Survey (NHBS) among People who inject drugs (PWID) and has continued to be used by the CDC and other investigators to evaluate trends in HIV and other health outcomes among PWID [37,39–47]. We chose this method as PWID are often well-networked and connected to other PWID in close geographic proximity [48], making network-based referrals an optimal recruitment method. Further, RDS often permits reach to individuals who are not engaged in health services.

Modified RDS began with an initial selection of approximately five seeds of well-networked PWUD, selected to maximize variation in ethnicity/race, age, and gender. Candidates were identified in each zone through conversations with staff during formative research (Aim 1). Seeds participate in study activities and refer up to three peers who will, in turn, be invited to participate in study activities and recruit others until the target sample size is reached. RDS is monitored in real-time to ensure that recruitment is progressing, identify and address bottlenecks, and monitor homophily in the study sample. New seeds are initiated if initial seeds are unproductive or recruitment slows. Given the evaluation focus rather than estimation of population prevalence that requires attention to specific assumptions, we used a modified approach that permits eligible individuals who approach the study staff but have not been referred by a seed/recruiter to enter the study as a seed themselves [36,37,49]. Seeds and recruiters receive secondary incentives of $5 per peer referral who completes the baseline survey. Paper and electronic coupons are provided to participants to facilitate referrals, with each coupon containing a unique code that allows for anonymous identification of the seed/recruiter as well as study branding and contact information to call and be screened for study inclusion. A form is established in our REDCap system to track recruitment information and coupon numbers from seeds and recruiters, and is built to mimic the RDS Coupon Manager [50], a common tool used for monitoring RDS.

Recruitment.

Once baseline recruitment begins, field staff walk around the area within 1–2 blocks, distributing recruitment cards to women on the street. Interested women are invited to return to the mobile RV to learn more about the study and be screened for eligibility if interested in a more private space.

To enroll in the study, the participants must be over 18, identify as a woman, and have used opioids or cocaine more than three times in the past week. Engagement with Mobile SPARC is not a requirement, as the study aims to assess the program’s community reach and impact. The intervention is introduced sequentially across the two zones, allowing a staggered rollout to manage resources for both SPARC and the study. SPARC services will continue beyond the study period.

Data collection.

Baseline and follow-up visits occur on the study van. After screening for eligibility and obtaining written consent, participants: 1) provide detailed locator information including phone numbers, addresses, email, social media accounts, and information for stable contacts; 2) complete a 45–60-minute audio computer-assisted self-interview (ACASI), with an interviewer available for assistance; 3) receive referrals to appropriate services, if desired; and 4) are compensated with a $50 visa gift card for their time. Each participant is assigned a unique ID. Regardless of whether they are in the intervention or control arm, all participants receive snacks and drinks, safer sex supplies (e.g., condoms), and safer drug use supplies (e.g., fentanyl test strips, naloxone).

In addition to standard demographics, the survey captures key outcomes related to overdose experiences and substance use history (past 6 months and 30 days), including type of drug used (or combination of drugs, e.g., fentanyl and cocaine), frequency, and routes of drug administration. Predisposing factors are assessed through socioeconomic status, housing stability, history of arrests, incarceration, and insurance status. Enabling factors include measures of healthcare access (primary care, specialty care, mental health providers, and substance use treatment), mental health status measured using the PHQ-9 for depression [51] and PCL-5 for PTSD [52], medical mistrust using an adapted Medical Mistrust Scale [53], and stigma using the Perceived Stigma of Substance Use [54] and Illicit Drug Use Stigma Scales [55]. Need factors focus on health priorities, comorbid conditions, and perceived care outcomes.

Cohort retention.

To maximize cohort retention, we will employ follow–up strategies that have proven effective in similar studies, achieving follow-up rates of 75–80% over 18 months [56]. At each visit, detailed locator information is collected and regularly updated to ensure successful ongoing contact with participants. The locator form captures each participant’s preferred method of communication, such as phone, text, social media, or via a stable contact, as well as their current address, a physical description, and contact information for at least two stable contacts who can receive messages on their behalf. Study staff utilize this information to make follow-up contact using a dedicated study Google Voice number, study email, and phone line.

In addition to remote outreach, staff use public databases, including the Maryland Inmate Locator, Maryland Case Search, and the Maryland Death Certificate Index, to help locate participants who are difficult to reach. Home visits to recorded addresses are also conducted when necessary. Printed study flyers are distributed as appointment reminders, and monthly updates are shared across study social media platforms to inform participants of upcoming follow-up activities in specific areas. To further support retention, staff maintain a consistent presence in recruitment areas throughout the study period.

Statistical data analysis.

The primary outcome analysis will examine whether the number of non-fatal overdoses during follow-up is lower for participants at the intervention sites versus the control sites, controlling for the number of non-fatal overdoses prior to baseline and adjusting for baseline covariates through inverse probability of treatment weights (IPTWs). The outcome model will use over-dispersed Poisson regression of counts of non-fatal overdoses adjusted for person-time at risk. Person-time for each participant will be the cumulative time intervals covered by questions about non-fatal overdose across the follow-up assessments. The primary independent variable will be whether a participant was enrolled from an intervention vs. control site, and, as intervention status is not randomly assigned, IPTWs will be used to improve exchangeability [57]. Participants in the intervention zones may differ from participants in the control zone at baseline in important ways that may affect or otherwise be associated with the likelihood of use of harm reduction services during follow-up and non-fatal overdose and other outcomes during follow-up.

IPTWs will be constructed from baseline covariates, including types, routes, and patterns of substance use, substance use treatment history, past overdose, demographics, employment, housing, physical health, mental health, and recent use of different harm reduction services, among other covariates. We will calculate standardized bias for baseline covariates as the difference in means or proportions between participants in the intervention and control sites, divided by the pooled SD for the covariate. Baseline covariates with standardized bias greater than 0.1 will be considered as candidates for bias reduction. Those variables and other baseline variables expected to be associated with the use of harm reduction services and overdose risk will be used as predictors in logistic regression of treatment status to generate IPTWs. We will then evaluate whether the weights have an acceptable distribution (e.g., mean approximately 1 and outliers limited through trimming of weights) and whether they are successful in reducing bias to an acceptable level (<.2 SD). If the IPTWs fail to achieve adequate balance on any baseline covariate for any site, we will consider including that baseline covariate as a fixed effect in the outcome analyses. Finally, we will conduct the outcome analyses with IPTWs to estimate the effect of the treatment vs. control site on cumulative non-fatal overdose and secondary outcomes.

Given that the intervention is hypothesized to affect overdose and other outcomes through the provision of harm reduction services, we will examine whether participants at the intervention sites versus the control sites are more likely to use harm reduction services during follow-up, controlling for use of harm reduction services prior to baseline and adjusting for baseline covariates using mixed effects models with IPTWs [58]. Observations (t) will be nested within participants (i), and the logistic models will include participant-level random intercepts, indicators for each follow-up assessment, group, group-by-follow-up interactions, and other baseline covariates. Whether treatment status is significantly associated with the use of harm reduction services will be evaluated through a simultaneous test of all group-by-follow-up coefficients.

Mixed effects models will also be used to evaluate the association of treatment status with other secondary outcomes, such as use of opioids and stimulants, injection drug use, syringe sharing, use of Test Strips, naloxone possession, intercourse without HIV pre-exposure prophylaxis (PrEP) or condoms, and unmet health or social services needs. The analytic approach will be the same as for the use of harm reduction services, but the link function and distributional assumption will be matched to the specific outcome.

SPARC staff interviews.

We will conduct semi-structured interviews with Mobile SPARC staff (N = 5–8) to gather insights into each RE-AIM domain. These interviews will focus on staff perceptions of Reach (who uses Mobile SPARC services), Effectiveness (impact of interventions on outcomes), Adoption (reflections on adoption in new neighborhoods and implementation factors influencing adoption), Implementation (process descriptions), and Maintenance (sustainability considerations). Eligible staff will include those with at least one outreach shift in the expanded service areas. Interviews will be conducted immediately post-18-month follow-up and will be audio recorded with consent; otherwise, detailed notes will be taken.

WWUD interviews.

We will purposively sample women who use drugs (N = 20) to represent a range of ages, races, and substance use histories. Eligible WWUD participants will have used Mobile SPARC at least once during the study. These in-depth interviews, done at the 18-month follow-up, will explore RE-AIM domains such as Effectiveness (extent to which services met needs), Adoption (benefits and areas for improvement), and Implementation (service interactions). Participants will receive a $40 Visa gift card for participation. Interviews will be audio-recorded, transcribed verbatim, and analyzed for consistency across domains.

Qualitative analysis.

Data from interviews will be analyzed thematically based on RE-AIM domains to identify factors influencing Mobile SPARC’s success. Analyses will focus on key aspects of service reach, unmet needs, and implementation facilitators, with findings guiding future Mobile SPARC service enhancements.

Cost analysis.

We will conduct a cost-effectiveness analysis to evaluate Mobile SPARC’s societal value, following guidelines from the 2nd US Panel on Cost-Effectiveness in Health and Medicine [59]. Using a micro-costing approach, we will assess resources utilized, including staff and participant contributions. Costs will be recorded at two intervention points, with a “best estimate” range to account for variability. We will determine cost-effectiveness by estimating the cost per visit and per person-year, informing effectiveness thresholds.

We will further estimate Mobile SPARC’s impact on health outcomes, utilizing quality-adjusted life years (QALYs) and participant-reported health states. Transmission models will estimate HIV and HCV incidence, informed by recent literature on health costs and QALYs. Outcomes will be evaluated based on societal willingness-to-pay thresholds, with sensitivity analyses examining parameter uncertainties and robustness.