Onsite Buprenorphine Treatment at Syringe Exchange Programs: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Onsite Buprenorphine Treatment at Syringe Exchange Programs (NCT03150173), a randomized phase 2 study. The primary outcome is Buprenorphine Engagement.

2. Clinical Question

This question concerns whether treatment initiation at a syringe exchange program is associated with a different level of early prescription engagement than enhanced referral. The registry record describes the trial as testing whether onsite initiation is more effective than referral, but the posted primary measure is specifically the count of participants with an active prescription at 30 days. It is a binary participant-level measure: each participant is categorized as having or not having an active prescription at that time.

3. Trial Design

The registry describes a completed Phase 2 randomized trial with a parallel-group design and no masking. The sponsor was Montefiore Medical Center, and enrollment was 97. The recorded start date was 2019-01-02, and the primary completion date was 2023-10-11. The population was syringe exchange participants with opioid use disorder in New York City.

Participants were assigned to O-BMT onsite treatment or enhanced referral. In the O-BMT arm, treatment began at the syringe exchange program, with provider visits and weekly blister packs during 2 weeks before transfer to a community health center for maintenance buprenorphine treatment. The comparator was enhanced referral to a community health center for maintenance treatment. Both arms therefore concerned access to buprenorphine treatment, with the initial location and route into care differing.

The registry labels allocation as randomized, masking as none, and the model as parallel. The primary analysis population is described as intention to treat, including participants lost to follow-up. The arm sizes reported for the primary outcome were 48 for O-BMT and 49 for enhanced referral. The registry record does not report the randomization sequence-generation procedure, allocation concealment, masking of outcome assessors, or detailed operational procedures for follow-up.

The primary outcome was buprenorphine engagement at 30 days after randomization, defined as having an active buprenorphine prescription. Secondary outcomes listed in the record include treatment retention, HIV risk behaviors, buprenorphine diversion, cost and quality-adjusted life-year measures, time to first prescription, and receipt of any prescription. The registry record does not report the original sample-size justification or the trial's detailed statistical analysis plan.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Before assignment: 211 participants were screened and 97 were randomized into the study. Of the 114 participants who were not enrolled into the study, 98 participants did not meet all of the eligibility criteria, 13 did not show up for the enrollment visit and 3 participants signed the informed consent form but were not randomized into the study.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Intention to treat (ITT) analysis design. All participants, including those who are lost to follow-up, are included in the analysis.

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

6. Primary Endpoint

The registry lists the primary outcome as Buprenorphine Engagement, measured over 30 days after randomization.

The primary endpoint is the number of participants with an active buprenorphine prescription 30 days after randomization. The registry describes it as a dichotomous Yes/No measure, summarized by study arm. A participant is counted as engaged if a prescription is active at the specified time point; the measure does not quantify the amount of medication taken or the continuity of treatment before or after that assessment.

This endpoint is used to assess early engagement with treatment. In this trial, it makes the comparison directly relevant to the difference between beginning care onsite and receiving enhanced referral. A prescription at 30 days is a concrete indicator that treatment has been initiated or maintained through that point, but it is not equivalent to confirmed medication use, longer-term retention, or a change in opioid use or HIV risk.

The record specifies an intention-to-treat analysis population and says that participants lost to follow-up remain included. It does not describe how missing prescription-status information was classified or otherwise handled. That detail matters because the endpoint is a yes-or-no status for each participant at a defined follow-up time. The posted counts are 19 in the O-BMT arm and 19 in the enhanced-referral arm, with arm denominators of 48 and 49, respectively.

7. Results Posted in the Registry

• Enhanced Referral: 38.8% (19/49) versus 39.6% (19/48) on control; risk difference -0.8 percentage points (95% CI -20.2 to 18.6), risk ratio 0.98 (0.60–1.61); unadjusted two-proportion z-test p = 0.935.

8. Secondary Efficacy Endpoints

The registry also posts results for secondary outcomes. For each outcome below, the endpoint type, the test applied to the posted summary statistics, the result and its interpretation are given in turn. Secondary endpoints are usually not adjusted for multiple testing, so they support rather than confirm the primary finding.

Treatment Retention

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Enhanced Referral: 12.2% (6/49) versus 4.2% (2/48) on control; risk difference 8.1 percentage points (95% CI -2.7 to 18.9), risk ratio 2.94 (0.62–13.85); unadjusted two-proportion z-test p = 0.148.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Enhanced Referral and the control. The interval gives the range of effects that remain compatible with the data.

HIV Risk Behaviors

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Enhanced Referral: 10.0% (4/40) versus 13.9% (5/36) on control; risk difference -3.9 percentage points (95% CI -18.5 to 10.7), risk ratio 0.72 (0.21–2.48); unadjusted two-proportion z-test p = 0.600.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Enhanced Referral and the control. The interval gives the range of effects that remain compatible with the data.

Buprenorphine Diversion

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Enhanced Referral: 4.1% (2/49) versus 16.7% (8/48) on control; risk difference -12.6 percentage points (95% CI -24.5 to -0.7), risk ratio 0.24 (0.05–1.09); unadjusted two-proportion z-test p = 0.042.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Enhanced Referral than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes add context to the primary prescription-engagement endpoint, but they do not create a single consistent pattern across all domains. The registry lists treatment retention, HIV risk behaviors, diversion, costs, quality-adjusted life-years, time to first prescription, and receipt of any prescription among its secondary measures. The posted results cover a range of outcomes and methods, with estimates that vary in direction and precision.

These outcomes concern different aspects of treatment and participant experience. Retention at 6 months is not the same endpoint as having an active prescription at 30 days; HIV risk behavior and diversion are separate binary outcomes; and cost or time-to-prescription measures address other questions. They can complement the primary result, but none changes what the primary endpoint itself measures. The secondary findings therefore should not be read as a single confirmation or contradiction of the primary comparison.

Unadjusted secondary results carry less weight because multiple outcomes and comparisons create more opportunities for a chance finding. The registry record does not report a multiplicity adjustment, a prespecified hierarchy among secondary endpoints, or which analyses were intended to be confirmatory. A secondary p-value should consequently be considered alongside its outcome definition, event count, analysis method, interval, and the broader set of outcomes, rather than in isolation.

Some secondary measures have fewer observations than the primary comparison, and sparse counts can produce uncertain estimates. The record does not explain all differences in denominators or provide a complete account of missingness for each outcome. Secondary results are informative as descriptive and exploratory evidence, but the available record does not support treating every nominal result as an independent confirmatory conclusion.

Secondary outcomes registered for this trial, for reference (only those above were recalculated):

• Treatment Retention
• HIV Risk Behaviors
• Buprenorphine Diversion
• Incremental Cost-effectiveness Ratio (ICER)
• Quality-adjusted Life-years (QALYs) Gained
• Mean Difference in Total Costs
• Time to First Buprenorphine Prescription
• Number/Percentage of Participants Who Received Any Buprenorphine Prescription

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary at the participant level: an active prescription at the 30-day assessment is recorded as yes or no. The registry reports the number meeting that definition in each arm, and the recalculation compares the proportion with the outcome in enhanced referral with the proportion in O-BMT. General explanation: a risk difference is the first group's outcome proportion minus the reference group's proportion. A value near zero indicates similar observed proportions; a positive or negative value indicates which group has the higher observed proportion according to the stated order.

What does the risk difference describe?

The posted primary risk difference is -0.008, with enhanced referral compared against O-BMT. Its sign indicates that the observed proportion in enhanced referral was slightly lower under that ordering. The estimate is close to zero, and the confidence interval extends from -0.202 to 0.186. The interval's inclusion of zero means that values compatible with no difference are among the estimates supported by this interval. The interval also spans differences in either direction, so the point estimate alone should not be treated as a definitive finding.

General explanation: a confidence interval gives a range of values compatible with the data under the method's assumptions. A wider interval indicates less precision than a narrower interval. It does not mean that every value inside the interval is equally likely, nor does it guarantee that the true effect falls within the interval. Interpretation also depends on whether the method is appropriate for the design and outcome.

What do the p-values add?

The registry reports a chi-squared test for the primary comparison, with p = 0.94. The unadjusted recalculation gives p = 0.935. A p-value describes how unusual data at least as discrepant as those observed would be under a specified null model, using the test's assumptions. It is not the probability that the null hypothesis is true, and it does not measure the size or importance of an effect. The primary p-value is consistent with the near-zero point estimate and interval spanning zero, but it cannot establish equivalence.

The posted secondary analyses use more than one method. Treatment retention is reported with a chi-squared test, HIV risk behaviors with logistic regression, and buprenorphine diversion with a Fisher exact test. General explanation: chi-squared procedures compare categorical outcome distributions; logistic regression models the odds of a binary outcome and can produce an odds ratio; Fisher exact testing evaluates categorical data using an exact probability calculation, which can be useful when counts are sparse. The registry's analyses and the unadjusted recalculations need not yield identical effect measures or p-values because their methods and estimands may differ.

Why distinguish odds ratios from risk differences?

A risk difference compares outcome proportions directly, whereas an odds ratio compares odds. These are distinct scales and should not be read as interchangeable. For HIV risk behaviors, the registry reports a logistic-regression odds ratio of 1.445, with a 95% confidence interval from 0.347 to 6.018 and p = 0.613. The unadjusted risk-difference recalculation for that outcome is a separate comparison and should not be interpreted as the same estimate expressed in different units. The registry record does not report enough detail to determine all covariates, coding choices, or model specifications for the logistic regression.

General explanation: odds and probability are related but not identical. An odds ratio of a stated size does not mean that the probability changes by the same amount. In addition, an odds ratio may be conditional on modeled covariates, while a simple risk difference is an unadjusted comparison. Readers should preserve the reported measure and method when describing each result rather than translating one into the other without the necessary information.

What does intention to treat mean in this record?

The primary analysis is labeled intention to treat and includes all participants, including those lost to follow-up. General explanation: intention-to-treat analysis aims to compare participants according to their randomized group, regardless of later treatment received or adherence. This approach preserves the randomized comparison in principle. The registry record does not state how missing outcome status was handled, whether outcome information was recovered from records for participants not otherwise followed, or whether any sensitivity analyses addressed missingness. Inclusion in the analysis population does not by itself explain how an unknown endpoint value was treated.

The primary endpoint is a count of participants with a binary event, not a continuous measurement. No dispersion measure is applicable in the posted primary data. The registry reports 12 outcome measures and 10 analyses, and it lists multiple secondary outcomes. General explanation: when several outcomes are tested, the chance of at least one apparently unusual result can increase if no adjustment or prespecified hierarchy is used. The registry record does not report a multiplicity strategy or identify which secondary comparisons were confirmatory. Secondary p-values should therefore be interpreted as exploratory unless a stronger prespecified framework is documented.

These methods describe the posted analyses, not necessarily the complete protocol. The original trial statistical plan, sample-size rationale, interim-analysis procedures, and further model diagnostics are not reported in the registry record. The separate sample-size illustrations are based on observed effects and stated planning assumptions; they are not a reconstruction of the trial's original design.

11. Confidence Intervals and Precision

The primary recalculated risk difference is -0.008, and its 95% confidence interval runs from -0.202 to 0.186. This interval includes zero and also extends to differences favoring either arm under the stated comparison order. The estimate is therefore not precise enough to rule out a range of potentially meaningful differences. The registry-reported chi-squared p-value is 0.94, while the recalculated unadjusted p-value is 0.935.

General explanation: precision concerns how narrowly an effect is estimated. A confidence interval expresses uncertainty around an estimate under the statistical method used. An interval that covers zero for a difference does not establish that the effect is exactly zero; it indicates that no difference is compatible with the interval as well as values in either direction. Conversely, an interval excluding zero does not by itself establish clinical importance or rule out bias.

The primary outcome has 19 events in each arm, with 48 and 49 participants in the respective groups. The near-equal event counts and similar group sizes accompany a point estimate close to zero, but the interval remains broad. The registry record does not report a prespecified smallest difference considered important, so statistical precision cannot be judged against a documented clinical threshold.

Secondary estimates are also uncertain. For example, the reported logistic-regression interval for HIV risk behaviors extends from 0.347 to 6.018 on the odds-ratio scale. Such a broad interval indicates limited precision for that modeled association. Sparse event counts in the secondary outcomes also make estimates sensitive to the chosen method. Confidence intervals should be read together with the endpoint definition, analysis method, and missing-data information, not as stand-alone declarations of effect.

12. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The sample-size illustrations describe planning scenarios based on the observed effect, not the trial's original design assumptions. The listed assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each scenario uses the stated fraction of the observed effect as the effect to detect. For binary outcomes such as those posted for this trial, the figures are participants per arm. The note about total events applies to time-to-event outcomes, not these binary outcomes.

The 80% power column gives the estimated participants per arm for a future study to have an 80% chance of detecting the selected effect under the stated assumptions, if that effect is real and the assumptions hold. The 90% power column describes the corresponding planning target for a 90% chance. These are planning illustrations, not observed power. They do not tell whether the completed trial had a particular probability of success after its results were known.

Each row changes the effect targeted relative to the observed effect. Planning for 75% of the observed effect requires more participants per arm than planning for 100% of the observed effect; planning for 50% requires more still. This follows the general statistical principle that smaller effects are harder to distinguish from random variation and therefore require larger studies, all else held constant.

For the primary outcome, the illustration for 100% of the observed effect gives 57,320 participants per arm for 80% power and 76,735 participants per arm for 90% power. The much larger figures in the smaller-effect scenarios reflect the fact that the observed primary difference is close to zero. These scenarios should not be treated as a recommended trial size: they inherit the observed estimate and the stated simplifying assumptions. The registry record does not report the original sample-size justification, its target effect, or its original power assumptions.

13. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

n is the number of participants in each arm, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.396; treatment proportion p₁ = 0.388; average p̄ = 0.392.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6903 = 1.3531.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6903 = 0.5810.
4. n = (1.3531 + 0.5810)² / (-0.0081)² = 57,319.8, rounded up to 57,320 participants per arm for 80% power.

The smaller-effect rows in the table above repeat the same calculation with the effect multiplied by 0.75 and 0.5 (for ratios, applied to the logarithm of the ratio).

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
p0 <- 0.395833333333333                          # control proportion
p1 <- 0.387755102040816                          # treatment proportion
n_per_arm <- function(power, frac = 1) {
  q1 <- p0 + (p1 - p0) * frac               # smaller effect = fraction of the observed difference
  pbar <- (p0 + q1) / 2
  z_b <- qnorm(power)
  ceiling(round((z_a * sqrt(2 * pbar * (1 - pbar)) + z_b * sqrt(p0 * (1 - p0) + q1 * (1 - q1)))^2 / (q1 - p0)^2, 6))
}
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: n per arm = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(n_per_arm(0.80, f), big.mark = ","), format(n_per_arm(0.90, f), big.mark = ",")))

# Check against R's built-in function (unrounded n per arm)
cat("power.prop.test:", round(power.prop.test(p1 = p0, p2 = p1, power = 0.80)$n, 1), "\n")

# Simulation: how often does the z-test reject at the 80%-power sample size?
set.seed(3150173)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 57,320 (80% power), 76,735 (90% power)
 75% of observed effect: n per arm = 101,996 (80% power), 136,543 (90% power)
 50% of observed effect: n per arm = 229,700 (80% power), 307,502 (90% power)
power.prop.test: 57319.8 
Simulated power at n = 57,320 per arm: 0.802 (20000 replicates)

The simulation draws many pairs of event counts at the planned sample size and counts how often the two-proportion z-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

14. Analyses Reported by the Sponsor

The registry's own primary analysis is a chi-squared test with p = 0.94. The unadjusted recalculation gives p = 0.935 and a risk difference of -0.008, with a 95% confidence interval from -0.202 to 0.186. The reported and recalculated p-values are close in magnitude, and both convey that the primary comparison does not show a clear difference. The recalculation also supplies an unadjusted effect estimate and interval based on the posted counts.

The sponsor's analysis is the registry-reported analysis and should be distinguished from the simple unadjusted recalculation. The registry record does not report enough detail to reconstruct every implementation choice behind the sponsor's test. The two p-values are not identical in their printed precision, so they should be quoted as reported rather than treated as the same numerical result. The recalculated risk difference and confidence interval are useful for expressing the size and uncertainty of the raw comparison, while the sponsor's test remains the posted trial analysis.

For secondary outcomes, the registry uses different methods depending on the endpoint. The unadjusted recalculations are not replacements for those analyses. In particular, the logistic-regression estimate and Fisher exact test address their outcomes using methods different from a simple risk-difference calculation. No discrepancy is flagged for the posted results, but methodological differences still matter when comparing estimates and p-values.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists multiple outcome measures and analyses, including the primary prescription-engagement outcome and several secondary measures. When many outcomes are examined, the chance of seeing at least one apparently notable result by chance increases. General explanation: a multiplicity plan can control or contextualize this problem through approaches such as a prespecified outcome hierarchy, adjusted testing, or clear designation of exploratory analyses. The registry record does not report whether any such approach was planned or used.

The record does not identify a detailed statistical analysis plan, an adjustment for multiple comparisons, or a prespecified hierarchy for the secondary outcomes. It is therefore not possible to determine from the registry record whether the reported secondary analyses were confirmatory or exploratory. Unadjusted secondary p-values should be interpreted cautiously and not as a collection of independent proofs.

The primary analysis population is described as intention to treat, including participants lost to follow-up. However, the method used to handle missing primary endpoint values is not reported in the registry record. Inclusion of every randomized participant in the intended population does not reveal whether missing statuses were treated as absent, imputed, recovered from other records, or addressed through another procedure. The record also does not report sensitivity analyses assessing the effect of missing outcomes.

Secondary outcome denominators differ across measures. The registry reports 36 and 40 participants for the HIV risk-behavior outcome, compared with 48 and 49 in the primary analysis. The reasons for these denominators and the handling of missing secondary data are not reported in the registry record. These differences limit direct comparisons between secondary outcomes and make it important to consider which participants contributed to each estimate.

The original sample-size rationale, interim-analysis procedures, stopping rules, and any prespecified subgroup analyses are not reported in the registry record. The separate planning illustrations use the observed effect and stated assumptions and do not fill in those missing design details. Without the original plan and fuller missing-data information, interpretation should remain focused on the outcomes and analyses explicitly posted.

16. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: skin infection (abscess) (2.1%), opioid overdose (2.0%), skin infection (methicillin-resistant staphylococcus aureus) (2.0%).

The registry lists serious adverse events for 1 participant in the O-BMT arm, with 48 at risk, and 2 participants in the enhanced-referral arm, with 49 at risk. It reports other adverse events for 2 participants in O-BMT and 1 in enhanced referral. Deaths are recorded as 0 in both arms. These are counts, and the registry record does not provide an arm-specific narrative explaining the events or their relationship to treatment.

The listed top serious-event terms are Skin Infection (Abscess) at 2.1%, Opioid Overdose at 2.0%, and Skin Infection (Methicillin-resistant Staphylococcus aureus) at 2.0%. The record does not specify in this summary which arm or arms contributed to each listed term, or how the percentages relate to the participant counts. They should therefore be read as registry-listed event terms rather than as a basis for assigning an event to a particular arm.

These figures are descriptive safety data. The small counts do not establish a comparative safety difference, and the registry record does not report detailed event severity, timing, attribution, or a formal statistical comparison. A lack of deaths in the posted counts does not answer broader safety questions beyond the recorded trial period and events.

17. What the Result Does, and Does Not, Mean

The main result is a comparison of active buprenorphine prescription status 30 days after randomization. The posted counts are 19 in each arm, and the unadjusted risk-difference estimate is close to zero. Its confidence interval spans zero and differences in either direction. The registry's chi-squared p-value is 0.94. Taken together, these data do not show a clear primary-outcome difference, but they also do not establish that the treatment pathways are equivalent.

The result is limited to the specified endpoint and follow-up time. An active prescription does not confirm how much medication a participant took, whether treatment continued beyond the assessment, or whether other health outcomes changed. The trial compared two approaches to reaching maintenance buprenorphine treatment: onsite initiation followed by transfer, and enhanced referral. It was not a comparison of buprenorphine treatment with no treatment.

The confidence interval is important because a near-zero point estimate can coexist with substantial uncertainty. The registry record does not report a threshold defining a clinically important difference or an equivalence margin. Without such a threshold and a design intended to test equivalence, a nonsignificant comparison should not be recast as proof that the approaches have the same effect.

The secondary findings address different outcomes and are not uniformly precise. They can help describe the breadth of outcomes recorded, but unadjusted secondary tests are less conclusive when the number of outcomes is large and no multiplicity plan is reported. Missing-data procedures and the original statistical plan are also not reported, which limits assessment of how robust the findings are to those choices.

Overall, the registry supports a narrow conclusion about the posted primary measure: the observed counts were equal, and the estimated difference is uncertain. It does not establish effects on long-term retention, HIV risk, cost-effectiveness, or other outcomes merely because those measures are listed. Nor does it settle whether the result generalizes beyond the trial's syringe exchange population and setting.

18. Why This Trial Matters Statistically

This trial raises a statistical question about how to evaluate an access pathway when both randomized groups are intended to reach maintenance treatment. The contrast is not treatment versus no treatment; it is onsite initiation followed by transfer versus enhanced referral. That makes the endpoint and comparator essential to interpreting the estimate. A difference in early prescription engagement would speak to the route into care at the chosen time point, not automatically to long-term clinical outcomes.

The primary result illustrates why effect estimates and confidence intervals matter alongside p-values. The p-value is not evidence that the arms are identical. The estimate is close to zero, but its interval spans differences in both directions. Statistical interpretation should distinguish a failure to show a clear difference from a demonstration of equivalence, especially when the registry record does not report an equivalence margin.

The posted secondary outcomes also illustrate the challenges of interpreting a broad outcome set. Different endpoints have different definitions, denominators, event counts, and analysis methods. A nominally unusual secondary result can be fragile when many outcomes are examined without a reported multiplicity plan. Presenting the result with its method and uncertainty gives a more faithful account than focusing on a single p-value.

Finally, the gap between the observed primary effect and the large planning illustrations emphasizes the relationship between effect size and required information. A small observed contrast is difficult to distinguish from random variation in a future study, and planning for smaller effects requires more participants under the stated assumptions. Those illustrations are not the trial's original design rationale. The record's missing design and analysis details are themselves relevant to how confidently readers can assess the evidence.

19. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

The posted primary result is imprecise: the 95% confidence interval for the unadjusted risk difference extends from -0.202 to 0.186. The registry record does not report a clinically important difference or equivalence margin, so the result cannot be judged against a prespecified threshold for practical importance. Equal event counts do not establish equivalence.

The endpoint captures active prescription status at 30 days, not verified medication use, duration of treatment, or a longer-term outcome. The intervention pathway includes an intended transfer to a community health center, but the record does not provide detailed adherence to that pathway or treatment receipt over time. The comparator is enhanced referral, so the contrast does not answer what would occur with no referral or no treatment access.

The registry record does not report the original sample-size justification, detailed statistical analysis plan, multiplicity procedures, interim analyses, missing-data methods, or sensitivity analyses. It also does not explain the lower denominators for some secondary outcomes. These omissions make it difficult to assess whether all planned analyses are represented and how missing information may affect estimates.

The trial is described as unmasked, but the registry record does not report whether outcome assessors were masked. It also does not give details of random-sequence generation or allocation concealment. These procedures cannot be inferred from the statement that allocation was randomized.

Secondary outcomes involve different measures and analysis methods, and some have sparse event counts. Their estimates may be unstable, and unadjusted testing across multiple endpoints increases the chance of chance findings. The safety information is also limited to posted counts and listed terms without detailed timing, attribution, or arm-specific event descriptions. These limitations call for restrained interpretation of both the primary and secondary results.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Onsite Buprenorphine Treatment at Syringe Exchange Programs — NCT03150173.
• Registry record last updated 2025-12-11; status last verified 2025-11.
• Results first posted 2025-01-14.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

The registry record describes NCT03150173, a completed Phase 2 randomized parallel-group trial sponsored by Montefiore Medical Center. It enrolled 97 syringe exchange participants with opioid use disorder in New York City and compared O-BMT onsite buprenorphine treatment with enhanced referral to a community health center. Masking was listed as none.

The primary endpoint was the count of participants with an active buprenorphine prescription 30 days after randomization. The reported counts were 19 in each arm. The unadjusted risk-difference estimate was -0.008, with a 95% confidence interval from -0.202 to 0.186; the registry-reported chi-squared p-value was 0.94.

The record also lists secondary outcomes and adverse-event counts. It does not report the original sample-size justification, detailed missing-data procedures, or a multiplicity plan. The primary result does not show a clear difference, and its uncertainty does not establish equivalence.