Phase 2, Double-Blind, Placebo-Controlled Trial of Bupropion for Methamphetamine Dependence: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Phase 2, Double-Blind, Placebo-Controlled Trial of Bupropion for Methamphetamine Dependence (NCT00687713), a randomized phase 2 study. The primary outcome is Number of Subjects Showing Abstinence.

2. Clinical Question

The clinical question concerns a defined treatment period and a specific behavioral outcome, rather than a broad measure of recovery or a long-term outcome. The registry describes treatment success as achieving two weeks of abstinence in the final two weeks of dosing. The posted primary counts are 14 participants in the bupropion group and 20 in the placebo group. Those counts are the observed results for the endpoint as defined in the record; they do not by themselves establish why the groups differed or whether the observed contrast is precise.

The trial also registered a secondary treatment-success outcome among subjects with 18 or less days of methamphetamine use. That outcome represents a related but distinct question. It should not be treated as interchangeable with the primary endpoint, which is defined by abstinence during Weeks 11 and 12. Neither outcome alone characterizes every aspect of participant experience, treatment adherence, or events after the treatment period.

3. Trial Design

The registry identifies this as a phase 2, randomized, parallel-group trial with triple masking and a placebo comparator. The listed sponsor is the National Institute on Drug Abuse (NIDA). The study is marked completed. Its recorded start was 2008-05, and its primary completion was 2011-05. These registry descriptors identify the broad trial structure; details about how randomization was implemented or which roles were included in triple masking are not reported in the registry record.

Participants were assigned to bupropion or matched placebo. The bupropion schedule began with a 150 mg tablet for 3 days, then twice daily for 12 weeks, with a taper during the last 3 days of week 12 at 150 mg per day. The placebo arm is described as following the matching schedule. The main outcome was assessed for Weeks 11 and 12, at the end of the dosing period. The registry also lists a secondary treatment-success outcome with a 30 days timeframe.

The registry lists a planned enrollment of 200. For the posted primary outcome, the arm counts are 100 for bupropion and 104 for placebo. The record does not explain the relationship between planned enrollment and the counts shown for the outcome, or report the number randomized, treated, or included in each analysis population separately. The original sample-size justification, recruitment details, allocation concealment procedures, and protocol deviations are not reported in the registry record.

Randomization can help balance measured and unmeasured participant characteristics across groups on average, while masking is intended to limit influences on care, reporting, and assessment. These are general design principles, not confirmation of the procedures used in practice. The registry does not describe the masking roles or whether masking was assessed. The parallel design means the groups are compared over the same study period, but details of visit schedules and how the endpoint was collected are not reported in the registry record.

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.

Overall Study

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 Number of Subjects Showing Abstinence, measured over Weeks 11 and 12.

The primary endpoint is the number of subjects showing abstinence, recorded as a count of participants. The registry defines treatment success as achieving two weeks of abstinence during the last two weeks of investigational product dosing, Weeks 11 and 12. Participants who did not achieve that defined success were scored as failures. The endpoint is therefore a binary participant-level outcome summarized as the count meeting the success definition in each group.

A binary endpoint is useful when the trial question is whether participants meet a prespecified clinical or behavioral criterion, rather than how much a continuous measure changes. It gives an interpretable count of successes, but it also compresses variation: participants who miss the criterion by different amounts are both categorized as failures under the stated definition. The endpoint does not, by itself, describe the frequency of methamphetamine use across the entire study or after dosing ended.

The posted primary outcome counts are 14 of 100 for bupropion and 20 of 104 for placebo. Counts should be read alongside the comparison estimate and its confidence interval, because the group totals differ and because a count alone does not quantify uncertainty about the contrast. The endpoint’s collection procedures, handling of missing assessments, and any rules for verifying abstinence are not reported in the registry record. These details matter for understanding how the binary success classification was applied.

7. Results Posted in the Registry

• Bupropion: 14.0% (14/100) versus 19.2% (20/104) on control; risk difference -5.2 percentage points (95% CI -15.4 to 4.9), risk ratio 0.73 (0.39–1.36); unadjusted two-proportion z-test p = 0.316.

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 Success Among Subjects With 18 or Less Days of Methamphetamine Use

• 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:
  • Bupropion: 65.0% (65/100) versus 73.1% (76/104) on control; risk difference -8.1 percentage points (95% CI -20.7 to 4.6), risk ratio 0.89 (0.74–1.07); unadjusted two-proportion z-test p = 0.212.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Bupropion and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists one secondary endpoint: treatment success among subjects with 18 or less days of methamphetamine use. It is related to the primary abstinence question but concerns a defined subgroup and a separate timeframe. The overall pattern of the posted comparisons is that the point estimates are in the direction of fewer successes with bupropion than placebo, while the intervals include values on both sides of no difference. This is broadly consistent with the uncertainty in the primary comparison rather than a clear reversal of its direction.

The secondary endpoint should be viewed as additional context, not as an independent confirmation of the primary result. Subgroup results can be less stable because they use a narrower population, and the registry does not report whether the subgroup was defined before results were examined or whether a formal interaction was tested. The record lists no reported analyses for the secondary outcome. Consequently, the arm counts and comparison should not be interpreted as a fully documented confirmatory analysis.

Unadjusted secondary results carry less evidential weight when multiple outcomes, groups, or analyses may be examined. General: Each additional statistical examination creates another opportunity for a seemingly unusual result to occur by chance, so interpretation commonly depends on a prespecified testing hierarchy or a multiplicity adjustment. No such strategy is reported in the registry record. The absence of an adjustment description does not prove that none was used, but it means the posted record does not establish that secondary inference was protected against multiplicity.

The secondary outcome can help describe whether a related success definition follows a similar broad pattern, but it cannot replace the registered primary endpoint or resolve its uncertainty. No claims about treatment effect within other subgroups, persistence beyond the outcome timeframe, or consistency across unreported analyses can be made from the registry record.

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

• Treatment Success Among Subjects With 18 or Less Days of Methamphetamine Use

9. Statistical Interpretation

10. Statistical Methods Explained

The posted primary comparison is a risk difference for a binary outcome. It contrasts the proportion meeting the abstinence definition in the bupropion group with the proportion in the placebo group. A negative estimate means the observed proportion is lower in the bupropion group under the stated ordering. This is a direct absolute comparison: it is expressed as a difference in probabilities, not as a ratio. The posted estimate is negative, while the confidence interval includes values on both sides of no difference.

What does a risk difference describe?

General: A risk difference is the event probability in one group minus the event probability in a reference group. Its zero value corresponds to equal event probabilities. Positive and negative values indicate opposite directions depending on the comparison order. Unlike a risk ratio, a risk difference is on an absolute scale, which can be useful for understanding how far apart the observed group probabilities are. The estimate remains subject to sampling uncertainty, especially when the event is uncommon or group sizes are limited.

The posted primary outcome is binary because each participant is classified as meeting or not meeting the two-week abstinence criterion. The registry provides event counts and group sizes, then gives a comparison estimate, interval, and unadjusted p-value. A count is not itself a probability or a treatment effect; the arm size provides the denominator needed for the group proportion. This explanation of the denominator is general, and no additional arm proportions are calculated.

How should the interval and p-value be read?

General: A confidence interval describes uncertainty around an estimate under a statistical procedure. Its endpoints indicate effect values that are compatible with the data and that procedure, conditional on its assumptions. An interval that includes the null value does not prove that the true effect is zero; it signals that the data do not exclude that value at the interval’s confidence level. The confidence level and interval method are not reported in the registry record, so the interval should be interpreted as posted without assuming a particular method.

The primary unadjusted p-value is 0.316. General: A p-value assesses the compatibility of the observed data with a specified null model, subject to the model and test assumptions. It is not an effect-size measure, does not give the probability that the null hypothesis is true, and does not establish whether an effect matters in practice. Because the record identifies the value as unadjusted, it should not be read as accounting for multiple outcome or subgroup examinations.

Why distinguish the estimate from statistical significance?

General: An estimate gives a direction and magnitude, while an interval communicates precision and a p-value summarizes evidence against a null hypothesis under a chosen test. These answer related but different questions. A result can have a directional point estimate yet remain uncertain; that is the pattern of the posted primary comparison. Interpretation should not reduce the result to a threshold decision based on the p-value alone. The record does not report a prespecified decision threshold or broader statistical analysis plan.

For binary outcomes, methods may be based on comparisons of proportions, regression models, or other approaches. The registry record does not report the method used to generate the comparison estimate, interval, or p-value. It also does not report covariate adjustment, stratification factors, clustering, or whether the primary analysis followed an intention-to-treat principle. No particular method should be inferred from the displayed statistics alone.

What is not established by the posted analysis?

The registry reports no analysis listings for the secondary outcome. The presence of arm-level counts and a comparison generated from those counts does not reveal whether a prespecified model was used, how missing outcomes were handled, or whether any additional analyses were conducted. The original statistical analysis plan, analysis populations, handling of protocol deviations, and interim analysis procedures are not reported in the registry record. These omissions limit assessment of whether the posted comparison fully reflects the planned analysis.

General: Randomization supports an unbiased comparison when allocation is implemented as intended and analyses preserve the randomized groups, but it does not automatically resolve missing data or deviations. Masking can reduce some forms of bias, but the registry’s triple-masking label does not describe who was masked or whether masking remained intact. These general principles explain why design labels are informative yet insufficient substitutes for procedural details.

The comparison is not described as adjusted in the record. Its p-value is explicitly unadjusted. There is no reported basis for treating it as corrected for multiple testing, and no sponsor analysis is described as taking precedence. The discrepancy indicator is false; this does not supply missing design details or establish which analysis methods were used. Overall, the methods that can be discussed are limited to the binary endpoint definition, posted group counts, and posted comparison statistics, with the unreported analytic details remaining unknown.

11. Confidence Intervals and Precision

The primary comparison’s confidence interval spans values below and above no difference. This means the posted data are compatible with a range of possible contrasts, including a lower success probability for bupropion, little or no difference, or a higher success probability. The point estimate is negative, but the interval’s breadth limits how firmly its direction can be interpreted. The interval does not establish that all values within it are equally plausible, nor does it guarantee that the true effect lies within it.

General: Precision concerns how narrowly an estimate is determined by the data under a statistical method. A narrower interval generally indicates greater precision than a wider interval, while still depending on the method and assumptions. The confidence level and construction method are not reported in the registry record. The interval should therefore be treated as the posted uncertainty range rather than interpreted as a specific confidence level or as a formal prediction for future participants.

The observed group counts are 14 of 100 for bupropion and 20 of 104 for placebo. The unadjusted p-value is 0.316. Neither the point estimate nor the p-value eliminates uncertainty about the underlying group difference. The p-value and interval answer different questions: the p-value summarizes compatibility with a null model, while the interval conveys a range of effect values consistent with the data and method. The available record does not report additional analyses that could show how robust precision is to alternative assumptions, missing-data handling, or covariate adjustment.

Precision also differs from clinical importance. Statistical uncertainty describes what the data can distinguish; it does not define which size of difference would matter to participants or clinicians. No threshold for a clinically important difference is reported in the registry record. Thus, the posted interval supports a cautious description of uncertainty, not a conclusion about the acceptability or practical significance of any particular value.

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 planning figures are participants per arm, not total event counts. The primary endpoint is binary, so the listed values are planning illustrations for participants in each of the two arms. The assumptions stated for the illustration are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect. The original trial’s own sample-size assumptions and justification are not reported in the registry record.

The 80% power column describes the number of participants per arm used in the planning illustration to give an 80% chance of detecting the assumed effect under the stated assumptions, if that effect and assumptions hold. The 90% power column uses a higher chance of detection and therefore requires more participants per arm for the same assumed effect. These are planning concepts, not guarantees about the result of a future study. This is not observed power.

The rows examine planning for 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect. For the primary outcome, the listed participants per arm for 80% power are 794, 1,457, and 3,375, respectively; the corresponding figures for 90% power are 1,063, 1,949, and 4,518. The illustration therefore shows the general pattern that smaller effects need more participants to detect under otherwise fixed assumptions.

The sample-size curve is a visual representation of those planning scenarios, not an account of the original trial design or a forecast of the outcome. The calculation is based on the observed effect, which is uncertain and may not represent the effect in another study. The posted figures should be interpreted as conditional planning illustrations rather than as evidence that the completed trial was adequately or inadequately sized.

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 = 0.192; treatment proportion p₁ = 0.140; average p̄ = 0.166.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5264 = 1.0317.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5251 = 0.4419.
4. n = (1.0317 + 0.4419)² / (-0.0523)² = 793.7, rounded up to 794 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 <- 0.192307692307692                          # control proportion
p1 <- 0.14                          # 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(687713)
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 = 794 (80% power), 1,063 (90% power)
 75% of observed effect: n per arm = 1,457 (80% power), 1,949 (90% power)
 50% of observed effect: n per arm = 3,375 (80% power), 4,518 (90% power)
power.prop.test: 793.7 
Simulated power at n = 794 per arm: 0.798 (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. Multiplicity, Missing Data and Analysis Populations

The registry identifies a primary endpoint and lists a secondary endpoint, but a full statistical analysis plan is not reported in the registry record. The record does not describe a multiplicity adjustment, testing hierarchy, or rule for interpreting secondary outcomes. The primary unadjusted p-value should therefore be read as an unadjusted comparison, rather than as evidence that accounts for every outcome or subgroup examined during the trial.

Missing-data procedures are not reported in the registry record. The endpoint is defined as a success or failure, but the record does not explain how participants with missing assessments, incomplete follow-up, or uncertain abstinence status were classified. It also does not describe imputation, sensitivity analyses, or assumptions about missingness. These choices can affect binary endpoint results because they determine which participants contribute to the success and failure counts.

Analysis populations are not reported in the registry record. The record does not identify whether the primary result represents all randomized participants, participants who received treatment, participants who completed treatment, or another defined group. It does not list exclusions after randomization or explain how protocol deviations were handled. The arm counts for the endpoint are shown, but those counts alone do not establish the analysis-population rule.

Interim analyses and stopping rules are not reported in the registry record. Nor are details of covariate adjustment, stratification, or prespecified subgroup analysis. These absences limit evaluation of how closely the posted analysis follows the intended plan and how much flexibility may have existed in selecting analyses. They should be treated as reporting limitations, not as evidence that a particular procedure was or was not used.

In general, multiplicity, missing-data, and analysis-population decisions affect the interpretation of estimates and p-values. A transparent report would make those choices explicit so readers could assess robustness and the intended role of each outcome. The registry record does not provide enough detail to make that assessment for this trial.

15. Safety Results

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

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 2% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: gastric bypass (2.9%).

The registry lists serious adverse events affecting 1 participant in the bupropion group, with 100 at risk, and 3 participants in the placebo group, with 104 at risk. The listed top serious-event term is Gastric bypass, at 2.9%. The record does not specify an arm for that term in the information available, so it should not be attributed to either treatment group. Death counts are not reported in the registry record.

These counts are descriptive safety information. They should be read with their group sizes and with the registry’s event definitions, which are not further detailed in the record. The counts alone do not establish that an event was caused by a study intervention, nor do they measure the full safety profile. Serious adverse events are distinct from the broader category of other adverse events; the registry lists 83 other adverse events in the bupropion group and 93 in the placebo group.

The record does not provide event narratives, timing, severity grading beyond the serious-event classification, relatedness assessments, or a detailed account of how events were collected. The posted figures therefore support a description of recorded counts, not a causal comparison or medical recommendation.

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

The posted primary result is a comparison of the number of participants meeting a defined abstinence criterion in the final two weeks of dosing. The bupropion group had 14 participants meeting that definition and the placebo group had 20. The risk-difference estimate points toward fewer successes with bupropion, but its confidence interval crosses no difference and the unadjusted p-value is 0.316. The data do not precisely establish the direction or size of the underlying difference.

This result does not show that the groups are equivalent. A non-significant unadjusted p-value is not proof of no effect, and the interval leaves room for possible contrasts in either direction. Conversely, the point estimate alone does not establish that placebo is superior or that bupropion is harmful. Statistical estimates describe the observed comparison and its uncertainty; they do not by themselves establish causation beyond the assumptions of the design and analysis.

The registry outcome applies to the stated population, treatment schedule, and assessment period. It does not answer whether results would be similar for people with other use patterns, under different dosing schedules, or over a different follow-up period. Longer-term outcomes, adherence, changes in use outside the defined abstinence window, and participant-level trajectories are not reported in the registry record.

The secondary endpoint offers related information but is not a substitute for the primary outcome, and the record does not report a multiplicity plan or secondary analysis listings. The posted results also do not provide enough detail to evaluate missing data, analysis populations, or the original sample-size justification. These gaps counsel against treating a single summary comparison as a complete account of efficacy or safety.

General: A trial result is most informative when interpreted together with its design, outcome definition, uncertainty, and reporting completeness. In this case, the registry supports a description of the primary counts and their imprecise comparison. It does not support medical advice, a definitive claim that treatment works or does not work, or a conclusion about an individual’s likely response.

17. Why This Trial Matters Statistically

This trial illustrates why a binary endpoint should be interpreted together with its comparison estimate and uncertainty, rather than through raw counts or a p-value alone. The primary outcome has a clear operational definition: two weeks of abstinence during Weeks 11 and 12. The registry reports the counts in both arms and a risk-difference comparison, making it possible to distinguish the observed direction from the uncertainty around that direction.

The result also shows why absence of a small p-value does not establish equality. The primary estimate points in one direction, while the confidence interval includes values on both sides of no difference. Statistical interpretation therefore requires attention to both the observed contrast and the range of values compatible with the analysis. Precision and clinical importance are separate questions, and the registry does not report a threshold for a clinically important difference.

Planning illustrations provide another useful statistical distinction. The sample-size figures are derived from the observed effect under stated assumptions; they are not the original design rationale and are not observed power. Their increasing requirements for smaller assumed effects illustrate a general relationship between effect size and planning needs. The original trial’s design assumptions remain unreported, so the illustration cannot establish whether the trial was planned to detect a particular effect.

Finally, the record demonstrates the importance of complete reporting. Details about missing outcomes, analysis populations, multiplicity, and statistical methods affect how readers assess robustness. Their absence does not justify guessing; it defines the limits of what can be concluded from the posted record. That distinction is important when statistical summaries are used to describe clinical trial evidence.

18. 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.

Several limitations are specific to the information recorded for this trial. Although the registry identifies randomization, triple masking, and a parallel design, it does not describe the randomization procedure, concealment, or which participants and study personnel were masked. The label alone cannot establish how those procedures were implemented or maintained.

The primary endpoint is defined as abstinence during Weeks 11 and 12, but the registry does not report how abstinence was assessed or verified. It also does not describe missing-assessment rules, adherence, participant flow, or the analysis population. Those omissions make it difficult to judge how the posted outcome counts relate to all randomized participants and how outcome classification was handled.

The registry lists planned enrollment as 200 and gives primary outcome counts of 100 and 104 in the two groups, but does not explain the relationship between those figures. It does not report the original sample-size justification, the target effect, or the statistical assumptions used when planning the trial. The planning illustration based on the observed effect does not fill that gap.

The record does not report the primary analysis method, adjustment variables, confidence-interval method, multiplicity strategy, interim analyses, or stopping rules. It also lists no reported analyses for the secondary endpoint. These omissions constrain assessment of analytic choices and the strength of secondary evidence. The results should therefore be interpreted as registry-posted outcome summaries, not as a complete clinical study report.

The follow-up period relevant to the primary endpoint is limited to Weeks 11 and 12, and longer-term outcomes are not reported in the registry record. The secondary outcome is also tied to a stated subgroup and timeframe. Generalization beyond the recorded eligibility description, intervention schedule, and outcome windows cannot be assessed from these data alone.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Phase 2, Double-Blind, Placebo-Controlled Trial of Bupropion for Methamphetamine Dependence — NCT00687713.
• Registry record last updated 2017-03-21; status last verified 2017-02.
• Results first posted 2017-02-15.
• 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.

22. Record Summary

NCT00687713 is a completed, randomized, parallel, triple-masked phase 2 trial comparing bupropion with matched placebo for methamphetamine dependence. The registry lists planned enrollment of 200 and describes the study population as subjects with dependence who reported methamphetamine use 29 or less days during the 30 days before signing consent.

The primary outcome was abstinence during Weeks 11 and 12. The posted counts were 14 of 100 for bupropion and 20 of 104 for placebo. The risk-difference estimate was negative, its confidence interval crossed no difference, and the unadjusted p-value was 0.316. The registry also lists a secondary treatment-success outcome among subjects with 18 or less days of methamphetamine use.

The record contains limited detail about statistical methods, missing data, analysis populations, multiplicity, and safety-event assessment. Those unreported elements limit conclusions beyond describing the posted counts, comparisons, and uncertainty.