Buprenorphine Extended-Release Subcutaneous Injection (RBP-6000) in High-risk Users: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Buprenorphine Extended-Release Subcutaneous Injection (RBP-6000) in High-risk Users (NCT04995029), a randomized phase 4 study. The primary outcome is Maintenance Phase: Percentage of Responders for Weekly Opioid Use Over Weeks 20 to 38.

2. Clinical Question

3. Trial Design

This completed phase 4 study, NCT04995029, was a randomized, double-blind, parallel-group trial sponsored by Indivior Inc. The registry lists enrollment of 785 participants. The study began on 2021-10-26, and primary completion was recorded as 2024-06-26. Its overall question covered both induction onto extended-release buprenorphine and maintenance dosing among treatment-seeking adults with opioid-use disorder and high-risk opioid use.

During induction, the rapid-induction group received 4 mg transmucosal buprenorphine on Day 1. Participants meeting eligibility requirements then received a 300 mg extended-release subcutaneous injection at least 1 hour later and a second dose on Day 8. The standard-of-care induction group received transmucosal buprenorphine for a minimum of 7 days, followed by 300 mg extended-release buprenorphine on Day 1 and a second dose on Day 8 if eligible. The registry record does not report comparative retention results for these induction strategies.

Participants eligible to continue treatment were randomized at Week 6 to maintenance injections of 100 mg or 300 mg every 4 weeks, for up to 8 injections from Weeks 6 to 34. The primary endpoint concerned response over Weeks 20 to 38. The primary analysis population was the Full Analysis Set: participants who met eligibility criteria, were randomized, and received at least one maintenance injection after double-blind randomization; participants were analyzed according to their randomized group. The registry record does not report the original sample-size justification or the detailed procedures used to maintain blinding.

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: Induction Phase: Participants were required to be in withdrawal (COWS score ≥8) to receive transmucosal (TM) buprenorphine (BUP). To receive RBP-6000, the participant did not display any allergic/ hypersensitivity reaction to TM BUP, did not experience precipitated withdrawal symptoms from the most recent TM BUP administration that would prevent RBP-6000 injection, and was not sedated. For standard of care, the participant had been dose-adjusted onto TM BUP for ≥7 days.

Induction Phase

Reasons for not completing this period:

Maintenance Phase

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The Full Analysis Set (FAS): Participants who met all inclusion/exclusion criteria, were randomized, and received at least 1 maintenance RBP-6000 injection post DB Randomization. Participants were analyzed according to the randomized treatment arm. This population served as the primary analysis population for efficacy analyses.

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.

Population: In the Induction Phase, of the 785 participants randomized (Substudy Randomized Population \[SRP\]), 729 were included in the Substudy Full Analysis Set (SFAS), the analysis set used for most endpoints and all safety analyses. Compared with the SRP, the SFAS excluded 56 participants: 48 who were randomized and inducted with neither rapid induction nor standard of care injection (which was a key protocol deviation) as well as 8 participants who discontinued prior to receiving TM buprenorphine.

6. Primary Endpoint

The registry lists the primary outcome as Maintenance Phase: Percentage of Responders for Weekly Opioid Use Over Weeks 20 to 38, measured over Weeks 20 to 38.

The primary endpoint is the number of participants meeting the definition of a responder for weekly opioid use over Weeks 20 to 38. A responder had opioid abstinence at at least 80% of visits in that interval. Abstinence required a negative urine drug screen together with a negative response about opioid use in the TimeLine Follow Back interview. That interview asked participants to estimate their daily drug use for the 7 days before each visit.

This endpoint translates repeated observations into a participant-level response classification. It is intended to capture a pattern of opioid abstinence across visits rather than a result from a single assessment. A participant who did not meet the response threshold was not counted as a responder, even if some visits showed abstinence. The endpoint therefore depends on both the visit-level assessments and the rule used to combine them.

The definition is operational: it specifies what was counted and over which interval. It does not, by itself, describe every aspect of opioid use between visits or resolve how unobserved assessments were handled. The registry record does not report the missing-visit rules for this endpoint. In the posted primary results, 44 of 218 participants in the 100 mg group and 50 of 216 in the 300 mg group were recorded as responders. These counts are the starting point for interpreting the comparison, alongside the sponsor’s reported analysis and its uncertainty interval.

7. Results Posted in the Registry

• Maintenance Phase: Extended-release Buprenorphine 300 mg: 23.1% (50/216) versus 20.2% (44/218) on control; risk difference 3.0 percentage points (95% CI -4.8 to 10.7), risk ratio 1.15 (0.80–1.64); unadjusted two-proportion z-test p = 0.453.

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.

Maintenance Phase: Percentage of Days Opioids Were Used Over Weeks 10 to 38

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Maintenance Phase: Extended-release Buprenorphine 300 mg: mean 15.90 versus 17.70 on control; difference -1.80 (95% CI -6.88 to 3.28), standardized effect d = -0.07; z-test p = 0.487.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Maintenance Phase: Extended-release Buprenorphine 300 mg and the control. The interval gives the range of effects that remain compatible with the data.

Maintenance Phase: Percentage of Responders for Weekly Opioid Use Over Weeks 10 to 38

• 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:
  • Maintenance Phase: Extended-release Buprenorphine 300 mg: 20.8% (45/216) versus 19.3% (42/218) on control; risk difference 1.6 percentage points (95% CI -6.0 to 9.1), risk ratio 1.08 (0.74–1.58); unadjusted two-proportion z-test p = 0.683.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Maintenance Phase: Extended-release Buprenorphine 300 mg and the control. The interval gives the range of effects that remain compatible with the data.

Maintenance Phase: Percentage of Visits With Opioid Abstinence Over Weeks 10 to 38

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Maintenance Phase: Extended-release Buprenorphine 300 mg: mean 32.10 versus 31.10 on control; difference 1.00 (95% CI -5.97 to 7.97), standardized effect d = 0.03; z-test p = 0.779.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Maintenance Phase: Extended-release Buprenorphine 300 mg and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists a broad set of secondary maintenance outcomes, including opioid-use frequency, abstinence at visits, responder status over different intervals, and use by injection route. The posted detailed comparisons include measures of percentage of days opioids were used, responder status over Weeks 10 to 38, and percentage of visits with abstinence over that interval. Across these available comparisons, the estimates are close to no difference relative to their uncertainty, and the reported intervals include no difference. This general pattern does not supply a separate, more decisive answer than the primary endpoint.

Secondary outcomes can help describe whether the primary result is consistent with other ways of measuring opioid use. However, measures may differ in their time windows, units, and response definitions, so they should not be treated as interchangeable replications. A direction that appears favorable on one measure may not persist across another, and an imprecise estimate may be compatible with effects in either direction.

The registry lists 17 secondary outcomes, while only some detailed secondary result comparisons are available in the posted results described by the record. Results for secondary outcomes without posted estimates are not reported in the registry record. The record also does not report whether multiplicity adjustment was applied. When many secondary hypotheses are considered, individual unadjusted p values carry less weight because chance findings become more likely across a collection of tests. These outcomes are most useful as contextual evidence and as a guide to questions for further study, rather than as a basis for overriding the primary analysis.

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

• Maintenance Phase: Percentage of Days Opioids Were Used Over Weeks 10 to 38
• Maintenance Phase: Percentage of Responders for Weekly Opioid Use Over Weeks 10 to 38
• Maintenance Phase: Percentage of Visits With Opioid Abstinence Over Weeks 10 to 38
• Maintenance Phase: Percentage of Responders for Weekly Opioid Use Over Weeks 30 to 38
• Maintenance Phase: Percentage of Responders for Daily Opioid Use
• Maintenance Phase: Percentage of Visits With Opioid Abstinence Overall
• Maintenance Phase: Percentage of Days Opioids Were Used Overall
• Maintenance Phase: Percentage of Days Opioids Were Used Via the Injection Route

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary at the participant level: each participant is classified as a responder or not under the registry’s definition. The displayed arm counts report the number of responders and the number of participants in each maintenance group. A treatment contrast for a binary endpoint can be expressed as a difference between response proportions, while a model-based analysis may account for factors used in stratification or other analysis features. The registry’s primary reported method is Cochran-Mantel-Haenszel (CMH), and its parameter is described as a CMH treatment difference.

What does the CMH analysis do?

In general, the Cochran-Mantel-Haenszel method combines comparisons across strata to produce an overall treatment contrast while accounting for the stratification structure. It can therefore differ from a direct, unadjusted calculation using only the overall arm counts. The registry record does not identify the stratification factors or describe the exact CMH implementation, so the specific adjustment cannot be reconstructed from the record alone.

The sponsor-reported primary estimate is 2.62, with a 95% confidence interval from -4.69 to 9.93. The corresponding p value is 0.482. A confidence interval describes a range of values compatible with the data and analysis assumptions; it is not a probability statement that the true effect lies in that particular interval. Because the reported interval includes zero, the analysis does not provide evidence of a clear difference under the sponsor’s method. The interval’s width also indicates that the estimate is not highly precise.

How does the recalculation differ?

The unadjusted re-calculation uses the posted responder counts and group sizes to estimate a risk difference without the stratified CMH approach. Its estimate is 0.030, its 95% confidence interval runs from -0.048 to 0.107, and its unadjusted p value is 0.453. This calculation is useful as a transparent check of the aggregate counts, but it does not reproduce a stratified analysis. The registry record identifies no discrepancy between the posted result and this recalculation; the sponsor’s reported analysis remains the principal analysis to interpret.

The p value describes how compatible the observed data are with a null hypothesis of no treatment difference, under the model and assumptions used. It does not give the probability that the null hypothesis is true, nor does it measure clinical importance. A non-small p value is not proof that the treatments are identical. Interpretation should consider the estimate, the confidence interval, the endpoint definition, and the analysis population together.

Why do analysis populations matter?

The record defines the Full Analysis Set as participants who met inclusion and exclusion criteria, were randomized, and received at least one maintenance injection after double-blind randomization. Participants were analyzed according to the randomized treatment arm. This describes who entered the primary analysis and the assigned-group principle, but it does not fully specify the treatment of participants with missing visits, incomplete assessments, or treatment discontinuation. Those procedures are not reported in the registry record.

For a repeated-visit endpoint, the participant-level response classification relies on information gathered over Weeks 20 to 38. The registry definition requires opioid abstinence at at least 80% of visits, based on urine testing and the TimeLine Follow Back interview. The record does not state how the denominator of visits was determined when visits were missed, or whether any imputation or sensitivity analysis was performed. These choices can affect a threshold-based outcome and its estimated contrast.

Why can over-dispersion matter?

Over-dispersion is a general concern when a model assumes more uniformity in binary outcomes than is present in the data. If participants’ outcomes vary more than the model allows, standard errors can be too small and confidence intervals too narrow. The registry record does not report a dispersion estimate for this binary primary endpoint, nor does it describe a model-based over-dispersion assessment. The point is therefore a general statistical consideration, not a claim that over-dispersion occurred in this trial.

Finally, the registry lists multiple outcomes and analyses. When many hypotheses are tested, the chance of obtaining an apparently notable result by chance can increase. The registry record does not report whether the primary and secondary analyses were adjusted for multiplicity or how the testing sequence was controlled. The primary analysis has a distinct role in the stated study objectives, while secondary comparisons should be interpreted with added caution unless an analysis plan establishing their inferential status is available.

11. Confidence Intervals and Precision

The sponsor’s primary estimate is 2.62, with a 95% confidence interval from -4.69 to 9.93. The interval includes zero and extends in both directions, so the posted data are compatible with a result favoring either maintenance group as well as with little or no difference. This range is more informative than the point estimate alone: it shows that the estimate has substantial uncertainty.

A confidence interval reflects sampling uncertainty under the analysis method and its assumptions. It does not account automatically for every possible source of bias, missing data, measurement error, or selective reporting. Nor does inclusion of zero prove equivalence. To support equivalence, an analysis would need a prespecified equivalence margin and a suitable design and inference; those details are not reported in the registry record.

The unadjusted recalculation from the posted counts gives a risk difference of 0.030 and a 95% confidence interval from -0.048 to 0.107. This interval likewise spans zero. Differences between this interval and the sponsor’s interval reflect that the sponsor reported a CMH analysis, whereas the recalculation is unadjusted and uses aggregate counts. Neither interval removes the central limitation that the observed comparison is imprecise.

Precision is also shaped by the number of participants contributing to the analysis and by variability in the measured outcome. The maintenance groups included 218 and 216 participants in the primary results. The record does not provide a trial-specific precision target, minimum important difference, or original sample-size justification. Consequently, the interval can be described statistically, but the registry record alone does not establish whether it is narrow enough to exclude differences that stakeholders would regard as important.

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 are planning calculations based on the observed effect, not the trial’s original design calculations. For the displayed binary and continuous outcomes, figures are participants per arm, not a total across both groups. The planning assumptions are a two-sided significance level of 0.05, equal allocation between two arms, a normal approximation, and an effect to detect set at the stated fraction of the observed effect. The registry record does not report the original design assumptions or sample-size justification.

The 80% power column gives the estimated number of participants per arm for a future study to have an 80% chance of detecting the specified effect under those planning assumptions, if that effect and the assumptions are correct. The 90% power column uses a higher probability of detecting that effect and therefore generally requires more participants per arm. These are prospective planning illustrations, not a description of the power achieved by this completed trial.

Rows describing planning for 100%, 75%, or 50% of the observed effect vary the assumed effect size. A smaller effect is harder to distinguish from random variation, so it requires more participants to reach the same target power. The illustrations are especially sensitive when the observed effect is small, because they scale planning around an estimate that is itself uncertain. They should not be treated as a guarantee that a future study with the listed enrollment would achieve the stated power.

For time-to-event outcomes, the planning convention is total number of events; the outcomes described in the available planning illustrations are not time-to-event outcomes. These figures are not observed power: observed power is not a useful substitute for interpreting the estimates and confidence intervals after a trial has been completed. The original design rationale, including any assumptions about expected treatment effects, attrition, or interim monitoring, is not reported in the registry record.

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 = 0.202; treatment proportion p₁ = 0.231; average p̄ = 0.217.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5826 = 1.1419.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5822 = 0.4900.
4. n = (1.1419 + 0.4900)² / (0.0296)² = 3,030.0, rounded up to 3,031 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 <- 0.201834862385321                          # control proportion
p1 <- 0.231481481481481                          # 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(4995029)
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 = 3,031 (80% power), 4,056 (90% power)
 75% of observed effect: n per arm = 5,321 (80% power), 7,123 (90% power)
 50% of observed effect: n per arm = 11,820 (80% power), 15,823 (90% power)
power.prop.test: 3030 
Simulated power at n = 3,031 per arm: 0.797 (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 sponsor’s primary analysis uses a Cochran-Mantel-Haenszel treatment difference. It reports an estimate of 2.62, a 95% confidence interval from -4.69 to 9.93, and p = 0.482. This is the trial’s own reported analysis and is the main result to use when describing the sponsor’s inference.

The unadjusted recalculation is based only on the posted responder counts and group sizes. It gives a risk difference of 0.030, a 95% confidence interval from -0.048 to 0.107, and an unadjusted p value of 0.453. It offers a check on the aggregate results, but it does not reproduce the CMH analysis or any stratification incorporated by that method. The small differences between the two analyses are therefore not, by themselves, evidence of an inconsistency.

The registry record indicates no discrepancy flag. The sponsor’s result and the unadjusted recalculation both have confidence intervals spanning zero, but the sponsor’s own analysis takes precedence as the reported trial analysis. The record does not give enough detail about the CMH strata to independently reproduce that analysis from the posted summary statistics.

15. Multiplicity, Missing Data and Analysis Populations

The registry record reports a primary endpoint and numerous secondary outcomes, as well as multiple analyses. It does not report a multiplicity-control procedure, such as a hierarchy of tests, an adjustment to significance thresholds, or a designated confirmatory sequence. Without those details, the inferential status of the secondary comparisons cannot be fully assessed. Unadjusted secondary p values, where reported, should therefore be interpreted cautiously rather than as independent confirmation.

Multiplicity is a general statistical issue: testing many outcomes can increase the chance that at least one result appears notable by chance, even when no underlying differences exist. This concern does not mean every secondary result is uninformative; it means that estimates, intervals, outcome relevance, and consistency across measures deserve attention alongside p values. The registry record does not say whether analyses were prespecified in a protocol or statistical analysis plan in a way that would clarify which results were confirmatory.

The primary population is described as participants who met inclusion and exclusion criteria, were randomized, and received at least one maintenance injection after double-blind randomization. They were analyzed according to randomized group. This is useful information, but the record does not report detailed missing-data methods, how missed visits affected the responder definition, or whether sensitivity analyses were conducted. It also does not report how participants who discontinued maintenance treatment were handled in the endpoint analysis.

Those omissions matter because the primary outcome depends on assessments across Weeks 20 to 38. The registry definition uses the proportion of visits with abstinence, but the record does not explain how the number of expected or observed visits was handled when assessments were unavailable. Without the protocol or statistical analysis plan, it is not possible to determine whether missing outcomes were treated as nonresponse, imputed, excluded under a rule, or addressed through another procedure. Those methods are not reported in the registry record.

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 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: chronic obstructive pulmonary disease (0.9%), seizure (0.5%), pneumonia (0.5%), burns second degree (0.5%), overdose (0.5%).

The registry lists serious adverse event counts separately for induction and maintenance groups. In rapid induction, 7 of 474 participants at risk had a serious adverse event; in standard-of-care induction, 1 of 255 did. In maintenance, 11 of 218 participants in the 100 mg group and 11 of 217 in the 300 mg group had a serious adverse event. These are registry counts and denominators, not adjusted comparisons of risk.

The registry also lists one death in the rapid-induction group and none in standard-of-care induction; the maintenance groups list none in the 100 mg group and one in the 300 mg group. Serious adverse events include different clinical events, and the record lists terms such as chronic obstructive pulmonary disease, seizure, pneumonia, second-degree burns, overdose, and skin laceration among the leading serious-event terms. The listed percentages range from 0.5% to 0.9% for those terms.

These counts should be read descriptively. The registry figures do not establish that a regimen caused an event or that a difference between groups is meaningful. The safety denominator for the 300 mg maintenance group is 217, while the primary efficacy results list 216 participants in that group; the registry record does not explain the difference. Event timing, exposure duration, and detailed attribution are not reported in the registry record.

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

The primary result describes a comparison of two maintenance doses among participants who reached maintenance, were randomized, and received at least one maintenance injection. It does not answer whether rapid induction differs from standard-of-care induction in treatment retention; those results are not reported in the registry record. It also does not describe every outcome of opioid use, because the primary endpoint reduces assessments over Weeks 20 to 38 to a responder classification.

The sponsor’s primary estimate and confidence interval do not establish a clear difference between the maintenance regimens on the defined responder outcome. At the same time, the interval includes possible effects in either direction, so the result should not be presented as proof that the doses are equivalent or that any difference is absent. The registry record does not provide an equivalence margin or a minimum difference considered important.

The responder definition combines urine drug screening and self-reported use from the TimeLine Follow Back interview. These assessments provide a specified way to classify abstinence at visits, but the record does not report how missing visits were handled or whether the classification captures opioid use between visits. The result is therefore tied to the definition and available measurements, rather than a complete account of each participant’s experience over the study.

Secondary outcomes provide additional descriptions of opioid-use patterns, but the registry record does not report multiplicity procedures, and not every listed secondary outcome has detailed results in the record. They should not be used selectively to make stronger claims than the primary analysis supports. Likewise, serious adverse event counts are descriptive and do not alone establish causation or comparative safety.

The interpretation is limited to the trial population and the reported analysis. The registry record describes treatment-seeking adults with moderate to severe opioid-use disorder and high-risk opioid use, but it does not provide all characteristics needed to judge how closely the analyzed participants resemble other populations. Clinical decisions require broader evidence and individual context; the statistical result alone is not a recommendation about treatment.

18. Why This Trial Matters Statistically

This trial illustrates the distinction between a numerical difference and a well-supported treatment contrast. The responder counts are not identical across groups, but the sponsor’s estimate is accompanied by an interval that includes zero and extends in both directions. Reading the estimate and its precision together avoids treating a point estimate as a definitive conclusion.

It also shows why the endpoint definition is central to interpretation. A participant-level responder threshold turns repeated assessments into a binary outcome, which can be easy to communicate but may conceal variation in the number and timing of abstinent visits. The result depends on the specified cutoff, the weeks assessed, the urine testing, and the self-report measure. Missing-data rules are especially relevant for this kind of outcome, yet they are not reported in the registry record.

The comparison is a maintenance-dose question within a larger study that also included an induction comparison. Separating these questions prevents the maintenance findings from being mistaken for evidence about induction retention. The reported sample sizes for the maintenance efficacy groups are also distinct from the larger overall enrollment and from the safety denominators.

Finally, the registry provides both a sponsor analysis and aggregate counts that permit an unadjusted recalculation. These serve different purposes: the reported CMH analysis is the sponsor’s primary analysis, while the recalculation is a transparent check based on the overall counts. Neither should be detached from the design, analysis population, and confidence interval. This is a useful example of why statistical interpretation depends on methods and reporting details, not only on whether a p value crosses a threshold.

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 registry record leaves several trial-specific details unavailable. It does not report the original sample-size justification, the expected effect used in planning, or the assumptions behind the planned enrollment. The posted planning illustrations are retrospective calculations based on observed effects and should not be confused with the study’s original design rationale.

The primary analysis is described as using the Full Analysis Set and analyzing participants according to randomized arm after receipt of at least one maintenance injection. The record does not report detailed handling of missing visits, treatment discontinuation, or incomplete urine and interview assessments. That is a notable limitation for a responder endpoint built from visits across Weeks 20 to 38.

The registry does not identify the stratification factors for the CMH analysis, so the sponsor’s primary calculation cannot be reproduced from the posted aggregate counts alone. The record also does not report a multiplicity plan, a prespecified equivalence or non-inferiority margin, interim analyses, or a detailed statistical analysis plan. These absences limit assessment of the full inferential framework.

Results for the induction-phase retention objective are not reported in the registry record. Although secondary outcomes are listed, the detailed comparisons available in the record cover only some of them. The maintenance efficacy and safety denominators also differ for the 300 mg group, with 216 in the primary results and 217 in the safety results; an explanation is not reported in the registry record.

Finally, the primary population is defined by eligibility, randomization, and receipt of at least one maintenance injection. The registry record does not provide sufficient participant-level characteristics or follow-up detail to judge the effects of selection into maintenance or generalizability beyond the enrolled population. These reporting gaps do not invalidate the posted estimate, but they constrain what can be concluded from it.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Buprenorphine Extended-Release Subcutaneous Injection (RBP-6000) in High-risk Users — NCT04995029.
• Registry record last updated 2026-02-06; status last verified 2026-01.
• Results first posted 2025-09-25.
• 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

NCT04995029 was a completed, randomized, double-blind, parallel-group phase 4 study of induction and maintenance strategies using extended-release buprenorphine in treatment-seeking adults with moderate to severe opioid-use disorder and high-risk opioid use. The registry lists enrollment of 785 participants. The primary maintenance comparison was 100 mg versus 300 mg every 4 weeks among eligible participants randomized at Week 6.

The primary endpoint was responder status for weekly opioid use over Weeks 20 to 38, defined by opioid abstinence at at least 80% of visits. The sponsor-reported CMH treatment difference was 2.62, with a 95% confidence interval from -4.69 to 9.93. The interval includes zero and remains compatible with effects in either direction. The registry record does not report induction retention results or several details needed to assess missing-data and multiplicity procedures.