A Phase 1/2 Trial of Multiple Oral Doses of OPC-167832 for Uncomplicated Pulmonary Tuberculosis: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Phase 1/2 Trial of Multiple Oral Doses of OPC-167832 for Uncomplicated Pulmonary Tuberculosis (NCT03678688), a randomized phase 1, phase 2 study. The primary outcome is Stage 1: Change From Baseline in TB Bacterial Load in Sputum as a Measure of Early Bactericidal Activity (EBA).

2. Clinical Question

This was a dose-ranging and combination-evaluation trial, not a single comparison of one regimen against one control. Its posted primary endpoint concerns Stage 1 only. The registry describes multiple doses of OPC-167832, then combinations in Stage 2; consequently, the primary endpoint results do not directly summarize the Stage 2 combinations.

The clinical question is also bounded by the short endpoint timeframe: the primary measure covers baseline to Day 14. It captures the rate of change in sputum bacterial burden during the initial treatment period, rather than a long-term clinical outcome. The registry record does not report a primary clinical outcome such as later disease status. The study also evaluated safety, tolerability, pharmacokinetics, and other bacterial measures, but those are distinct questions from the primary EBA comparison.

3. Trial Design

NCT03678688 is a completed, randomized, open-label Phase 1/2 trial sponsored by Otsuka Pharmaceutical Development & Commercialization, Inc. The registry lists enrollment of 122 participants. The recorded start date is 2018-10-18, and the primary completion date is 2022-02-14. Allocation is described as randomized, masking as none, and the model as sequential. The registry record does not report further details of the sequence-generation or allocation-concealment procedures.

Stage 1 included OPC-167832 dose groups of 3 mg, 10 mg, 30 mg, and 90 mg, as well as RHEZ. Participants in the OPC-167832 groups received the assigned dose once daily from Day 1 through Day 14, followed by RHEZ according to the local standard of care regimen up to Day 20. The Stage 1 RHEZ group received RHEZ once daily from Day 1 through Day 20. RHEZ contains rifampicin, isoniazid, pyrazinamide, and ethambutol, with the component amounts described in the registry record.

Stage 2 examined 30 mg OPC-167832 with 300 mg delamanid, with 400 mg BDQ, or with both delamanid and BDQ. A Stage 2 RHEZ group is also listed. The combination regimens are described as being administered during the initial treatment period, followed by RHEZ; some Stage 2 arm descriptions in the registry record are truncated, so the incomplete details are not expanded.

The trial was open-label, so participants and study personnel were not masked according to the registry. This matters when interpreting outcomes that might involve judgment or reporting, although the primary endpoint is based on sputum culture measurements. The registry record does not report the trial’s original sample-size justification, detailed randomization procedures, or a full 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: Participants with uncomplicated, smear-positive, drug-susceptible pulmonary tuberculosis were enrolled in two stages. Stage 1: A total of 76 participants were randomized in 4 cohorts to receive either OPC-167832 10 milligrams (mg), 30 mg, 90 mg \& 3 mg or a combination of rifampicin, isoniazid, ethambutol, and pyrazinamide (RHEZ). Stage 2: A total of 46 participants were randomized in 4 groups to receive OPC-167832+delamanid, OPC-167832+bedaquilline (BDQ), OPC-167832+delamanid+BDQ or RHEZ.

Only the first 6 of 9 groups are shown.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: MITT Analysis Set included randomized participants who were agar media culture positive at baseline (either at Day -2 or at Day -1, or both), received any dose of IMP, and had at least one post-baseline CFU count value. Overall number analyzed is the number of participants with data available for 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.

Population: Randomized Analysis Set included participants who were randomized into the trial.

Only the first 6 of 10 groups are shown.

6. Primary Endpoint

The registry lists the primary outcome as Stage 1: Change From Baseline in TB Bacterial Load in Sputum as a Measure of Early Bactericidal Activity (EBA), measured over Baseline to Day 14.

The primary endpoint is Stage 1 change from baseline in TB bacterial load in sputum, used as a measure of early bactericidal activity. Bacterial load was assessed using CFU counts on agar media culture. The registry defines EBA as the rate of decline per day in log10CFU/mL during the first 14 days of treatment, and defines change from baseline as the post-baseline value minus the baseline value. The stated unit is sputum log10CFU/mL, and the timeframe is baseline to Day 14.

This type of short-term microbiological measure is used to describe how bacterial burden changes during initial treatment. It can support comparisons of early activity across dose groups, but it is not the same as a long-term clinical outcome. The registry’s description says that a larger EBA in the positive direction indicates a better drug effect. Because the posted arm summaries are mean changes and are negative, they should be read in the context of the endpoint’s specific sign convention and calculation; the mean change alone is not interchangeable with the EBA rate as defined in the endpoint description.

The primary analysis population was the MITT Analysis Set: randomized participants who were agar media culture positive at baseline, received any dose of investigational product, and had at least one post-baseline CFU count value. The registry record’s description of the population is cut off after this definition, and additional handling of missing or unusable measurements is not reported in the registry record.

7. Results Posted in the Registry

• Stage 1: 30 mg OPC-167832: mean -2.12 versus -1.93 on control; difference -0.19 (95% CI -2.95 to 2.57), standardized effect d = -0.05; z-test p = 0.893.
• Stage 1: 90 mg OPC-167832: mean -2.08 versus -1.93 on control; difference -0.15 (95% CI -2.57 to 2.27), standardized effect d = -0.05; z-test p = 0.903.
• Stage 1: 3 mg OPC-167832: mean -1.69 versus -1.93 on control; difference 0.24 (95% CI -2.72 to 3.20), standardized effect d = 0.06; z-test p = 0.874.
• Stage 1: RHEZ: mean -2.79 versus -1.93 on control; difference -0.86 (95% CI -3.55 to 1.83), standardized effect d = -0.24; z-test p = 0.531.

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.

Stage 1 and Stage 2: Change From Baseline in Time to Detection (TTD) in the MGIT System

• 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:
  • Stage 1: 30 mg OPC-167832: mean 9.54 versus 4.28 on control; difference 5.26 (95% CI -2.93 to 13.45), standardized effect d = 0.57; z-test p = 0.208.
  • Stage 1: 90 mg OPC-167832: mean 18.15 versus 4.28 on control; difference 13.87 (95% CI 5.55 to 22.19), standardized effect d = 1.30; z-test p = 0.001.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Stage 1: 30 mg OPC-167832 and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Stage 1: 90 mg OPC-167832 than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Stage 2: Cmax of DM-6705

• 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:
  • Stage 2: 30 mg OPC-167832 + 300 mg Delamanid + 400 mg BDQ: mean 14.60 versus 10.30 on control; difference 4.30 (95% CI -4.04 to 12.64), standardized effect d = 0.39; z-test p = 0.312.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Stage 2: 30 mg OPC-167832 + 300 mg Delamanid + 400 mg BDQ and the control. The interval gives the range of effects that remain compatible with the data.

Stage 2: Cmax,ss of DM-6705

• 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:
  • Stage 2: 30 mg OPC-167832 + 300 mg Delamanid + 400 mg BDQ: mean 112.00 versus 84.00 on control; difference 28.00 (95% CI -6.71 to 62.71), standardized effect d = 0.67; z-test p = 0.114.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Stage 2: 30 mg OPC-167832 + 300 mg Delamanid + 400 mg BDQ and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary outcomes span microbiological measures and pharmacokinetic measures. They include change in time to detection in the MGIT system, change in LAM in the MGIT system, Stage 2 change in TB bacterial load, plasma rifampin concentration, Stage 1 plasma isoniazid concentration, and measures of DM-6705 exposure. The set is broader than the primary endpoint and addresses different biological and pharmacokinetic questions.

The available secondary results show variation in both estimated values and dispersion across groups. For time to detection, for example, the displayed Stage 1 means range from 3.33 to 18.15 days, and the standard deviations vary substantially. The posted comparisons include a 90 mg versus 10 mg estimate of 13.87 days, with a 95% confidence interval from 5.546 to 22.19 and an unadjusted p-value of 0.001. The 30 mg versus 10 mg comparison has a 95% confidence interval from -2.935 to 13.45 and an unadjusted p-value of 0.208. These secondary observations are distinct from the primary mean-change endpoint and do not resolve its uncertainty.

Stage 2 pharmacokinetic summaries also compare combinations with and without BDQ for DM-6705 measures. Their estimates have confidence intervals that span zero, and their sample sizes are limited. Those results describe pharmacokinetic measurements, not the primary Stage 1 bacterial-load contrast. The registry lists 56 outcome measures and 12 analyses overall; only 17 secondary outcomes are posted as secondary results. The status of results not posted is not reported in the registry record.

Unadjusted secondary comparisons carry less evidential weight when many outcomes, arms, or contrasts are considered, because the chance of seeing apparently unusual findings can increase across repeated testing. This is a general statistical concern, not evidence that a particular finding is false. The registry record does not report a multiplicity strategy for the secondary outcomes. Secondary results are therefore most useful as descriptive and hypothesis-generating context, and should not be treated as independent confirmation of the primary result.

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

• Stage 1 and Stage 2: Change From Baseline in Lipoarabinomannan (LAM) in the Mycobacteria Growth Indicator Tube® (MGIT) System
• Stage 1 and Stage 2: Change From Baseline in Time to Detection (TTD) in the MGIT System
• Stage 2: Change From Baseline in TB Bacterial Load in Sputum as a Measure of EBA
• Stage 2: Plasma Concentration of Rifampin
• Stage 1: Plasma Concentration of Isoniazid
• Stage 2: Cmax of DM-6705
• Stage 2: Cmax,ss of DM-6705
• Stage 2: Tmax of DM-6705

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is continuous: it records change in sputum bacterial load on a log10CFU/mL scale. The registry gives a mean for each arm and reports standard error as the measure of dispersion. A mean describes the central value across participants with available endpoint data. Standard error describes the uncertainty in estimating that mean; it is not the same as the spread of individual participant measurements.

What does a mean difference express?

General explanation: a mean difference subtracts the average in one group from the average in another, using a specified reference group and direction. It expresses the contrast in the endpoint’s units. The recalculated contrasts use the 10 mg OPC-167832 group as reference. Their sign depends on which group is subtracted from which, so the sign should not be read as a standalone statement about benefit. It must be interpreted alongside the endpoint definition and direction.

These are unadjusted recalculations from the posted arm summaries. They are not the sponsor’s own analysis and do not incorporate a covariate-adjusted model or other adjustments unless those are explicitly described in the registry record. The recalculated results include a mean difference, confidence interval, and unadjusted p-value for each listed contrast. The registry record does not report the sponsor’s method for the EBA ratio analyses, and the recalculations do not replace those analyses.

What does a confidence interval convey?

General explanation: a confidence interval describes uncertainty around an estimate under the assumptions of the method used to calculate it. A wider interval indicates less precision than a narrower interval. For a difference, an interval spanning zero does not rule out a null difference at the corresponding confidence level. It can also include differences in either direction. The interval alone does not establish that one group is equivalent to another; equivalence requires a defined margin and an analysis designed to assess that question.

The primary arm summaries report standard errors, while the recalculated comparisons use pooled standard deviations derived from the posted summaries for their planning illustrations. The pooled standard deviation describes variability on the scale used in the planning calculation. It is not a separately observed endpoint or an additional trial result. The planning illustrations use the observed recalculated effect as their starting point and consider smaller fractions of that effect.

Why can small groups produce uncertain estimates?

General explanation: with limited observations, an estimated mean or group contrast can shift noticeably when individual observations vary. This uncertainty is represented by the standard error and reflected in the confidence interval. Small groups do not make a result invalid, but they can leave a wide range of effect sizes compatible with the data. The Stage 1 analyzed groups are small relative to the planning figures calculated from the observed contrasts, so the recalculated comparisons should not be treated as precise estimates of a stable effect.

Why does over-dispersion matter?

General explanation: over-dispersion means observed variation is greater than a model’s assumptions allow. When that occurs, standard errors and confidence intervals from a model that understates variability can be too small, making estimates appear more precise than warranted. The registry record does not report an over-dispersion assessment or a count-based model for the primary endpoint. The primary endpoint is presented as a continuous mean measure with standard error, so no claim about over-dispersion is made for these results.

How should p-values be read?

General explanation: a p-value quantifies how unusual data at least as discrepant as the observed data would be under a specified null model and its assumptions. It does not measure the probability that a treatment effect is true, nor does it measure clinical importance. The recalculated p-values are unadjusted, meaning they do not account for the number of comparisons. They should be considered alongside the estimated differences and intervals rather than used as a standalone decision rule.

The registry record lists multiple doses and multiple endpoints, making the broader analysis context important. The full prespecified testing sequence, any multiplicity adjustment, and any interim analyses are not reported in the registry record. Consequently, the posted unadjusted results should be interpreted as exploratory evidence unless the registry documents a confirmatory testing plan.

11. Confidence Intervals and Precision

Precision is limited for the primary endpoint comparisons. The recalculated 95% confidence intervals are broad: for the 30 mg versus 10 mg contrast, -2.948 to 2.568; for 90 mg versus 10 mg, -2.569 to 2.269; for 3 mg versus 10 mg, -2.721 to 3.201; and for RHEZ versus 10 mg, -3.549 to 1.829. Each interval spans zero and includes differences in both directions. In practical statistical terms, the posted summaries do not tightly pin down the size or direction of these mean contrasts.

The arm standard errors also indicate uncertainty around the reported means: 0.98 for 10 mg, 1.01 for 30 mg, 0.75 for 90 mg, 1.15 for 3 mg, and 0.96 for RHEZ. These are standard errors of the means, not ranges containing most individual participants. The analyzed sample sizes, which range from 10 to 14 across these arms, are relevant context for the uncertainty.

The sponsor’s analyses are reported as EBA ratios with 95% confidence intervals. For 10 mg versus RHEZ, the posted estimate is 0.689, with two reported intervals, 0.485 to 0.939 and 0.467 to 0.911. For 30 mg, the estimate is 0.759, with intervals 0.517 to 1.051 and 0.497 to 1.020. For 90 mg, the estimate is 0.745, with intervals 0.567 to 0.973 and 0.547 to 0.943. For 3 mg, the estimate is 0.605, with intervals 0.353 to 0.896 and 0.338 to 0.871. The registry record does not identify why two intervals are posted for each estimate or specify their analysis methods. That missing detail limits direct interpretation of their precision.

Confidence intervals describe sampling uncertainty under the method used; they do not cover every source of uncertainty, such as differences in analysis choices, missing data, or limited generalizability. The registry record does not provide enough detail to assess those sources fully.

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 illustrations based on the recalculated observed effect, not the trial’s original design calculation. For these continuous outcomes, each figure is the number of participants per arm. The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each row considers an effect equal to the observed effect or a stated fraction of it. The trial’s own original sample-size assumptions and justification are not reported in the registry record.

The 80% power column means the illustrated number of participants per arm under the stated assumptions for a design with an 80% chance of detecting the selected effect, if that effect is the true one and the model assumptions hold. The 90% power column applies the same idea with a higher chance of detecting that effect. These are prospective planning concepts, not probabilities that the posted trial result is correct.

Smaller effects are harder to distinguish from random variation, so the planning calculations require more participants as the assumed effect decreases. For example, the RHEZ comparison’s illustration lists 280 participants per arm for 80% power and 375 for 90% power when using 100% of the observed effect; the corresponding values for 50% of that effect are 1,119 and 1,498. These figures are not proposed enrollment requirements for the trial, and they do not imply that these group sizes would address every design issue.

These values are planning illustrations, not observed power. Observed power is not a useful substitute for interpreting the observed estimate and its confidence interval; precision and uncertainty are better read from the interval and the amount of data available.

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, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = -0.190; pooled standard deviation σ = 3.481.
2. n = 2 × (1.96 + 0.842)² × 3.481² / -0.190² = 5,269.5, rounded up to 5,270 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
delta <- -0.19                      # observed difference in means
sigma <- 3.48112964946203                     # pooled standard deviation
n_per_arm <- function(power, frac = 1) {
  ceiling(round(2 * (z_a + qnorm(power))^2 * sigma^2 / (delta * frac)^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 (t-based, so very slightly larger)
cat("power.t.test:", round(power.t.test(delta = delta, sd = sigma, power = 0.80)$n, 1), "\n")

# Simulation: exact two-sample t-test using simulated means and variances
set.seed(3678688)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 5,270 (80% power), 7,055 (90% power)
 75% of observed effect: n per arm = 9,369 (80% power), 12,542 (90% power)
 50% of observed effect: n per arm = 21,079 (80% power), 28,218 (90% power)
power.t.test: 5270.5 
Simulated power at n = 5,270 per arm: 0.802 (20000 replicates)

The simulation draws many sets of group means and variances at the planned sample size and counts how often the two-sample t-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 posted primary analyses compare each OPC-167832 dose with RHEZ using EBA ratios. The simple recalculations instead compare arm means using mean differences, with the 10 mg OPC-167832 arm as reference. Because the reference groups and effect measures differ, the two analyses answer related but nonidentical questions. Their estimates should not be expected to match numerically.

The registry reports EBA ratio estimates and 95% confidence intervals for the dose-versus-RHEZ comparisons, but no p-values or analysis methods are listed. Two different confidence intervals are posted for each ratio estimate. The registry record does not explain the distinction between those intervals, so the method and intended interpretation of each are not reported in the registry record.

The recalculated mean differences are simple, unadjusted computations from posted summary statistics. They are useful as a transparent comparison of the displayed arm means, but they do not supersede an analysis conducted by the sponsor using participant-level data and its intended model. The discrepancy flag is false, so there is no recorded conflict requiring the sponsor’s own analysis to take precedence over a recalculation. Even so, the sponsor’s analysis remains the registry’s reported analysis, while the recalculation is a separate summary-based analysis with different contrasts.

Neither set of results should be interpreted without its estimand, reference group, endpoint definition, and uncertainty. Because details of the sponsor’s statistical method are absent, the registry record does not permit a full assessment of how its ratio results were produced or how they relate to the mean-change summaries.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when a study examines several doses, outcomes, time points, or pairwise comparisons. As the number of tests increases, the chance of at least one apparently unusual result can rise even when there is no underlying effect. General statistical approaches include prespecifying a testing hierarchy, adjusting significance thresholds, or presenting results as exploratory. The registry record does not report whether any such approach was used for the primary or secondary analyses.

The study includes several Stage 1 dose groups, Stage 2 combinations, and multiple outcome measures. The record lists 56 outcome measures and 12 analyses. These counts do not establish which tests were confirmatory, which were planned for formal inference, or whether all analyses were reported. A multiplicity adjustment or a prespecified primary comparison is not reported in the registry record. The simple recalculated p-values are unadjusted, and should not be interpreted as if they account for all comparisons made in the trial.

The primary analysis population is described as randomized participants who were culture positive at baseline, received any dose of investigational product, and had at least one post-baseline CFU count. This definition gives useful information about who could contribute primary data. However, the full population description is truncated in the registry record. The number excluded from this analysis and reasons for exclusion are not reported in the registry record.

Missing-data procedures for the primary endpoint are not reported in the registry record. It is not reported how unavailable post-baseline measurements, incomplete follow-up, or deviations from assigned treatment were handled in the analysis. The registry also does not report interim analyses, stopping rules, a detailed analysis plan, or how the sequential model affected the timing or selection of arms. These omissions limit assessment of whether the posted analyses followed prespecified procedures and how robust the results are to alternative assumptions.

Randomization can reduce confounding on average, but the open-label design and small analyzed groups remain important context. Baseline characteristics by arm and an assessment of balance are not included in the registry entries. Their values and any adjustment for them 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 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: anal abscess (7.7%), pneumothorax (7.7%), haemoptysis (7.1%).

The serious adverse event counts are presented by arm, alongside the number at risk. In Stage 1, there were no serious adverse events in the 10 mg, 30 mg, or 90 mg groups, one in the 3 mg group, and none in the RHEZ group. The listed numbers at risk were 14, 14, 17, 14, and 16, respectively. In Stage 2, there were no serious adverse events in the delamanid combination or the combination with both delamanid and BDQ; two were reported in the OPC-167832 plus BDQ group, with 13 at risk. No serious adverse events were reported in the Stage 2 RHEZ group, with 4 at risk. Deaths were listed as zero in every group.

These are event counts, not estimates of comparative risk. The group sizes are small and differ between the safety listings and the primary endpoint analysis, so the counts should not be read as precise comparisons between regimens. The registry lists serious-event terms including Anal abscess, Pneumothorax, and Haemoptysis, each with a posted percentage of 7.7%, 7.7%, and 7.1%, respectively. The record does not give enough information to assign those terms to particular groups or establish causality.

The non-serious adverse-event listings report affected participants by group, but do not provide event-level detail in the registry entries. Serious adverse events, other adverse events, and deaths are distinct categories; their counts should not be combined. These summaries describe what was posted and do not establish comparative safety.

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

The results describe a small, randomized, open-label Phase 1/2 study of multiple OPC-167832 doses and combination regimens in participants with uncomplicated, smear-positive, drug-susceptible pulmonary tuberculosis. The primary endpoint focuses on Stage 1 change in sputum bacterial load through Day 14. The arm means and recalculated comparisons provide a short-term microbiological description, while the broad confidence intervals show that the simple mean contrasts are not estimated precisely.

The posted primary data do not establish equivalence among doses, nor do they provide a precise ranking of groups by the recalculated mean differences. An interval that includes zero is compatible with a range of possible differences, and an unadjusted p-value is not a probability that the null hypothesis is true. The sponsor’s ratio analyses address a different comparison and metric; their methods are not specified in the registry record. These distinct analyses should not be collapsed into one claim.

The endpoint is an early bactericidal activity measure, not a long-term clinical outcome. Results from baseline to Day 14 do not by themselves establish what happens after the initial treatment period, and they do not answer every question about safety, tolerability, pharmacokinetics, or later disease outcomes. Stage 2 combination arms also cannot be inferred from the Stage 1 primary endpoint results.

Enrollment of 122 applies to the trial overall, whereas primary endpoint group sizes range from 10 to 14. The total enrollment should not be mistaken for the number contributing to each primary contrast. Nor should planning illustrations be read as actual observed power or as evidence that the trial was designed around those recalculated effects.

Overall, the registry record supports a cautious descriptive reading: it documents the trial’s arms, endpoint, posted summaries, and selected analyses, but it does not provide all details needed to reconstruct the complete analysis strategy. These data are not, by themselves, a basis for a medical decision or a general conclusion about treatment efficacy.

18. Why This Trial Matters Statistically

This trial is statistically informative because it combines dose-ranging work with a sequential evaluation of drug combinations, while reporting an early microbiological endpoint. That structure creates several distinct estimands: dose contrasts within Stage 1, comparisons with RHEZ, and pharmacokinetic or microbiological comparisons within Stage 2. Keeping those questions separate is essential. A result from one stage or outcome cannot automatically be transferred to another.

The trial also illustrates how a point estimate can appear straightforward while its uncertainty remains substantial. The Stage 1 mean changes are posted alongside standard errors, and the recalculated comparisons have broad intervals. Reading the estimated direction without its interval would overstate what the available data establish. Likewise, a p-value alone does not reveal whether an effect is precisely estimated or clinically important.

Open-label randomized studies can still provide useful early evidence, especially when outcomes are measured objectively, but their interpretation depends on the analysis population, measurement procedures, and prespecified comparisons. The primary endpoint is based on culture measurements, yet details such as missing-data handling and the full analysis plan are not reported in the registry record. The absence of those details limits reproducibility and makes it harder to judge how firmly the analyses were planned in advance.

The planning illustrations are another useful statistical lesson: a sample-size calculation based on a small observed effect can yield very large hypothetical group sizes. That does not imply the original trial should have enrolled those numbers. It shows how planning depends on the effect one wants to detect and the assumptions used. The registry record does not report the original design rationale, so these calculations should remain separate from claims about the trial’s design.

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.

Several limitations are specific to the information posted for this trial. First, the trial is open-label and has multiple doses, stages, combinations, and outcomes. Although the primary endpoint is based on culture counts, the registry record does not report masking, detailed measurement quality procedures, or an analysis plan that would clarify how these features were addressed.

Second, the primary endpoint analysis groups are small, with analyzed sample sizes from 10 to 14. The recalculated confidence intervals are broad. This limits precision and means that the data can be compatible with a range of differences. The overall enrollment of 122 does not remove the uncertainty in a particular arm comparison, because the primary endpoint is reported for smaller analysis groups.

Third, the registry record does not report the original sample-size assumptions, missing-data procedures, interim analyses, multiplicity strategy, or reasons participants may have been excluded from the primary analysis set. It also does not report the statistical method behind the sponsor’s EBA ratio analyses. Two confidence intervals are listed for each ratio estimate without an explanation of their difference. These gaps prevent a complete review of the analysis choices.

Fourth, some Stage 2 arm descriptions are truncated, and the available primary endpoint results apply to Stage 1 rather than the Stage 2 combination regimens. The secondary results cover only part of the listed outcome measures. It is not reported in the registry record why the remaining outcomes are not posted.

Finally, the endpoint is a short-term microbiological measure through Day 14. It does not alone characterize later clinical outcomes. These limitations concern interpretation of the posted record; they do not determine the results of analyses or follow-up information that is not reported in the registry record.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Phase 1/2 Trial of Multiple Oral Doses of OPC-167832 for Uncomplicated Pulmonary Tuberculosis — NCT03678688.
• Registry record last updated 2023-11-18; status last verified 2023-10.
• Results first posted 2023-11-18.
• 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

NCT03678688 is a completed randomized, open-label Phase 1/2 trial with enrollment of 122 participants. It evaluated multiple oral doses of OPC-167832 in uncomplicated, smear-positive, drug-susceptible pulmonary tuberculosis, followed by Stage 2 combination regimens. The primary endpoint was Stage 1 change from baseline in sputum TB bacterial load as a measure of EBA, from baseline to Day 14.

The posted Stage 1 arm means range from -1.69 to -2.79, with standard errors from 0.75 to 1.15. Simple unadjusted mean-difference recalculations against the 10 mg group have broad 95% confidence intervals spanning zero. The sponsor’s reported EBA ratio analyses compare dose groups with RHEZ, but their methods are not identified in the registry record. Secondary findings address other microbiological and pharmacokinetic measures, while safety listings report few serious adverse events and zero deaths in all listed groups.

The registry record does not report the original sample-size rationale, multiplicity strategy, interim analyses, or missing-data procedures. The posted results therefore support a bounded, descriptive interpretation of early endpoint data rather than a complete assessment of all trial questions.