A Study to Determine the Fed Bioequivalence of Reformulated OXY Tablets and Original OxyContin® (OXY) Tablets: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study to Determine the Fed Bioequivalence of Reformulated OXY Tablets and Original OxyContin® (OXY) Tablets (NCT01099709), a randomized phase 1 study. The primary outcome is Cmax - Maximum Observed Plasma Concentration.

2. Clinical Question

3. Trial Design

This was a Phase 1, randomized, open-label, single-center, single-dose, two-way crossover study in healthy subjects. The two treatments were reformulated OXY 10 mg and original OxyContin® 10 mg, each given as one dose in the fed state. A crossover design means that participants receive more than one treatment in a planned sequence, allowing treatment responses to be compared within a participant. That general feature can reduce the influence of stable differences between people, but the registry record does not report the actual treatment sequences, washout interval, or other details of the dosing schedule.

The record lists enrollment of 85 and a completed study. The primary pharmacokinetic analysis population is defined as randomized subjects who received study drug and had at least one valid pharmacokinetic metric; subjects with emesis within 12 hours after dosing were excluded from that analysis. The endpoint results list 79 for reformulated OXY and 81 for original OxyContin®. These arm-level figures are reported as such; the registry does not explain the relationship between these analysis counts in enough detail to infer how many participants contributed paired data.

Masking was none, so the study was open-label. The registry records a primary completion date of 2007-03 and a start date of 2007-01. The primary outcome was Cmax, and blood sampling covered a 72-hour period. There were three outcome measures and four analyses recorded, while no secondary outcomes are posted in the results represented in the registry record. The record does not report a detailed protocol, a sample-size justification, original design assumptions, interim analyses, or a full statistical analysis plan. Those items should not be inferred from the observed results or from planning illustrations based on them.

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: 145 subjects screened; 48 screen failures; 12 alternates/early discontinuations; 85 randomized; 3 terminated early; 82 completed.

Period 1

Reasons for not completing this period:

Period 2

Analysis population for the primary outcome, as defined in the registry: Full Analysis Population for PK Metrics. Data from all subjects who were randomized, received study drug, and had at least 1 valid PK metric variable were included in the statistical analysis. Subjects who experienced emesis within 12 hours after dosing were excluded from PK analysis.

5. Baseline Characteristics

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

6. Primary Endpoint

The registry lists the primary outcome as Cmax - Maximum Observed Plasma Concentration, measured over Blood samples collected over 72-hour period.

Cmax is the maximum observed plasma concentration after a dose. It describes the peak concentration observed in the blood-sampling period, rather than the total amount of drug exposure over time. In this study, blood samples were collected over a 72-hour period, and the primary outcome was measured in ng/mL. The registry describes the endpoint as a mean with standard deviation and states that bioequivalence was based on Cmax.

General: pharmacokinetic comparisons commonly use measures such as peak concentration to assess whether two formulations produce similar concentration profiles. For bioequivalence, the comparison is often expressed as a ratio of the test formulation’s measure to the reference formulation’s measure. A ratio focuses on proportional rather than absolute differences and is often analyzed on a logarithmic scale. The registry reports a geometric test-to-reference ratio for Cmax, which is consistent with that kind of comparison.

Cmax is only one characteristic of drug exposure. It does not by itself describe every aspect of the concentration-time profile, and the posted primary endpoint does not answer questions beyond the measured pharmacokinetic comparison. The record does not report the bioequivalence acceptance limits, so the reported ratio and confidence interval can be interpreted numerically, but they cannot be independently compared with a criterion that is absent from the registry record.

7. Results Posted in the Registry

• Reformulated OXY (Test): mean 14.20 versus 13.60 on control; difference 0.60 (95% CI -0.29 to 1.49), standardized effect d = 0.21; z-test p = 0.187.

8. Statistical Interpretation

9. Statistical Methods Explained

The registry contains two kinds of statistical summaries for Cmax: group-level means and standard deviations, and a sponsor-reported geometric test-to-reference ratio with a confidence interval. An additional unadjusted recalculation compares the listed arithmetic means. Each answers a different statistical question, so the estimates should be kept distinct rather than combined into a single claim.

What does the mean difference describe?

General: a mean difference subtracts one group mean from another. It is expressed on the original measurement scale, which is ng/mL for Cmax. The posted means are 14.2 for reformulated OXY and 13.6 for original OxyContin®, yielding the reported recalculated difference of 0.6. A positive difference indicates that the listed mean for the test treatment is higher than the listed mean for the reference treatment. This direction describes the estimate; it does not by itself establish a meaningful difference or a bioequivalence result.

The recalculation is unadjusted and based on posted summary statistics. It is not the sponsor’s crossover-model analysis. A crossover analysis may account for the design and within-participant comparisons; the registry identifies an ANOVA for the ratio analysis, but does not report enough model detail to reconstruct that analysis. The difference calculation therefore offers a separate, simple comparison and should not be treated as a substitute for the reported bioequivalence analysis.

What does a standard deviation describe?

General: a standard deviation describes the spread of individual observations around a mean. It is not the uncertainty in the mean itself and is not a confidence interval. The listed standard deviations are 2.99 for reformulated OXY and 2.75 for original OxyContin®. In a crossover study, the variability of within-person differences can be important for inference, but the arm-level means and standard deviations do not provide that paired variability. The registry record does not report it in the results represented.

How should the confidence interval be read?

General: a confidence interval expresses uncertainty around an estimate using a method with a stated long-run coverage property. The recalculated mean-difference interval is a 95% interval, from -0.291 to 1.491. It gives a range of values compatible with that unadjusted calculation under its assumptions. It is not a range containing a specified proportion of individual participants’ values, and it does not account for details that are unavailable from the posted summary statistics.

The sponsor-reported interval is different: it is a 90% confidence interval for the geometric test-to-reference ratio multiplied by 100, with limits of 101.06 and 108.51. It is on a ratio scale rather than the original Cmax difference scale. A confidence interval’s interpretation depends on the estimate, scale, confidence level, and analysis method. The two intervals cannot be compared as if they were estimates of the same quantity.

Why is a ratio used in bioequivalence work?

General: pharmacokinetic measurements are often right-skewed, and ratios can be more natural for comparing exposure across formulations than absolute differences. A log transformation turns ratios into differences on the analysis scale; results can then be expressed back as geometric ratios. The registry labels the sponsor’s analysis as a geometric test/reference ratio multiplied by 100 and lists ANOVA as its method. The record does not provide model terms, transformation details, or the precise estimation procedure, so those should not be inferred.

Bioequivalence is not simply a failure to find a statistically significant difference. General: equivalence is usually evaluated by comparing a confidence interval for a treatment ratio with prespecified lower and upper acceptance limits. If the full interval falls inside the limits, it supports the criterion defined by those limits. The registry does not report those limits. Without them, the ratio and its interval can be described but not independently classified against the intended threshold.

Why can over-dispersion matter?

General: over-dispersion occurs when observed variation is greater than a statistical model expects. If a model understates variation, confidence intervals may be too narrow and tests may appear more decisive than warranted. If variation is modeled appropriately, uncertainty estimates better reflect the data. No over-dispersion issue is reported for this trial, and the posted summary statistics do not allow an assessment of whether it was relevant. The concept is therefore a general methodological consideration, not a finding about this study.

The registry reports an open-label crossover design but does not provide full model specifications. It also does not report the treatment sequence, washout interval, or within-subject covariance. These details matter to a complete independent reconstruction of a crossover analysis. The posted calculations should therefore be read according to what they are: the sponsor’s reported geometric-ratio analysis and a separate unadjusted recalculation from summary statistics.

10. Confidence Intervals and Precision

The recalculated mean difference in Cmax is 0.6 ng/mL, with a 95% confidence interval from -0.291 to 1.491. This interval spans zero, which means the unadjusted calculation is compatible with no difference in arithmetic means as well as with positive mean differences. Its width also indicates that the estimate is not precise enough to isolate a single value. The interval describes uncertainty about the mean difference under the recalculation’s assumptions; it does not describe the spread of individual Cmax measurements.

The sponsor-reported geometric test-to-reference ratio multiplied by 100 is 105, with a 90% confidence interval from 101.06 to 108.51. That interval is on a different scale and uses a different confidence level from the recalculated mean-difference interval. Its limits describe uncertainty around the ratio estimate, not an absolute change in ng/mL. The registry does not report the acceptance limits required to judge the interval against the study’s bioequivalence criterion.

General: precision depends on the amount of information in the data and the variability of the measure, among other factors. In a crossover study, within-participant variability is particularly relevant to a paired treatment comparison. The registry’s arm-level summary statistics do not give the variability of paired differences, so the recalculated interval cannot reflect all the design information that may have been used in the sponsor’s analysis. Neither interval should be read as proving equality or as a prediction interval for an individual subject’s response.

11. 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 events. They are illustrations based on the observed effect, rather than a reconstruction of the study’s original design. The registry record does not report the trial’s original sample-size assumptions or justification. The planning calculation assumes a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each planning row uses a stated fraction of the observed effect as the effect to detect.

The 80% power column describes the planned number of participants per arm for a design that would have an 80% probability of detecting the specified effect under the stated assumptions, if that effect and model assumptions held. The 90% power column gives the corresponding planning number for a design with a 90% probability under those assumptions. These percentages describe prospective operating characteristics of a hypothetical design; they are not the probability that the observed result is correct. This is not observed power.

The planning rows use 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect. The associated figures rise as the effect fraction becomes smaller: for 100% of the observed effect, the figures are 360 participants per arm for 80% power and 482 participants per arm for 90% power; for 75%, they are 639 and 856; for 50%, they are 1,438 and 1,925. Smaller effects need more participants because they are harder to distinguish from random variation under the same assumptions. These are planning illustrations, not observed sample sizes and not proof of the trial’s achieved power. They should not be interpreted as recommendations for a new study without a design-specific rationale.

12. 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 = 0.600; pooled standard deviation σ = 2.871.
2. n = 2 × (1.96 + 0.842)² × 2.871² / 0.600² = 359.4, rounded up to 360 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 <- 0.6                      # observed difference in means
sigma <- 2.8709895528647                     # 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(1099709)
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 = 360 (80% power), 482 (90% power)
 75% of observed effect: n per arm = 639 (80% power), 856 (90% power)
 50% of observed effect: n per arm = 1,438 (80% power), 1,925 (90% power)
power.t.test: 360.4 
Simulated power at n = 360 per arm: 0.798 (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.

13. Analyses Reported by the Sponsor

The registry reports the sponsor’s analysis as an ANOVA-based geometric test-to-reference ratio multiplied by 100. The reported ratio is 105, and its 90% confidence interval is 101.06 to 108.51. This is the analysis explicitly reported for the bioequivalence comparison. The registry also lists a separate recalculated comparison of arithmetic means: a difference of 0.6 ng/mL, a 95% confidence interval from -0.291 to 1.491, and an unadjusted p-value of 0.187.

These results are not contradictory simply because their values and intervals differ. They estimate different quantities, use different scales, and do not share the same confidence level or analysis method. The recalculation uses posted summary statistics and is unadjusted; it does not reproduce the sponsor’s crossover analysis. The registry does not report full model details or the acceptance limits for bioequivalence. Thus the sponsor analysis should be read as the registry’s reported bioequivalence result, while the recalculation is an additional descriptive comparison, not a replacement for it.

The registry record does not flag a discrepancy between the posted and recalculated results. The available information does not support a fuller audit of the sponsor’s analysis, because model specifications and bioequivalence limits are not reported in the registry record.

14. Multiplicity, Missing Data and Analysis Populations

The registry lists three outcome measures and four analyses, but no secondary outcomes are posted in the results represented in the record. Cmax is identified as the primary outcome. The record does not report a complete statistical analysis plan, a multiplicity adjustment, or how any family of outcome tests was defined. It is therefore not possible to determine from the registry record whether the analyses were treated as a single testing family or whether any adjustment was planned or applied.

General: multiplicity arises when several hypotheses or outcomes are tested. Repeated testing can increase the chance of at least one apparently notable result even when no corresponding effect exists. Adjustments or a prespecified hierarchy can address that issue, but the method depends on the scientific questions and analysis plan. No particular multiplicity procedure should be attributed to this trial based on the information recorded.

The primary pharmacokinetic population is described as randomized subjects who received study drug and had at least one valid pharmacokinetic metric. Subjects who experienced emesis within 12 hours after dosing were excluded from PK analysis. The registry record does not report how many subjects were excluded for emesis, the number with missing endpoint data, or detailed reasons for any missing values. The arm-level endpoint counts are 79 and 81; these are not sufficient by themselves to reconstruct the full participant flow or determine whether missingness was related to treatment or outcome.

Because the study used a crossover design, paired observations and within-participant structure are relevant. The record does not report the paired-data count, treatment sequence details, washout interval, or a detailed missing-data method. It also does not report sensitivity analyses for excluded or missing observations. Those omissions limit independent assessment of how the endpoint analysis handled incomplete data. They do not establish that the analysis was inappropriate; they mean the registry record does not contain enough detail to evaluate these aspects fully.

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 5% reporting threshold.

Most frequent non-serious adverse event terms

The registry lists zero serious adverse events among 83 at risk in the reformulated OXY 10-mg fed group and zero among 84 at risk in the original OxyContin® 10-mg fed group. These are the serious-event figures recorded for the groups. They indicate that no serious adverse events were reported in either group in the posted results; they do not establish that serious events are impossible or that the treatments have identical safety profiles.

The record also lists other adverse events affecting 41 of 83 in the reformulated group and 29 of 84 in the original-formulation group. These are separate from the serious-adverse-event counts and should not be conflated with them. The registry does not list deaths for these groups. No serious adverse-event terms are listed among the top serious-event terms.

General: adverse-event counts need to be read in light of the study population, exposure, observation period, and event definitions. This was a single-dose study in healthy subjects, and the posted safety figures do not establish what may occur under other treatment conditions or in other populations. The record does not provide further event detail in the serious-event summary, so these counts are descriptive rather than a complete safety assessment.

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

The posted results describe a comparison of Cmax after single fed doses of reformulated OXY and original OxyContin® in healthy subjects. The mean Cmax values were 14.2 ng/mL and 13.6 ng/mL, respectively. The sponsor-reported geometric test-to-reference ratio multiplied by 100 was 105, with a 90% confidence interval from 101.06 to 108.51. These values summarize the pharmacokinetic comparison under the conditions recorded for this study.

The unadjusted recalculation gives a mean difference of 0.6 ng/mL and a 95% confidence interval from -0.291 to 1.491. Its unadjusted p-value is 0.187. This calculation does not establish equivalence; a test for a difference is not the same as an equivalence assessment. The sponsor’s ratio analysis is the relevant reported bioequivalence analysis, but the registry record does not report the acceptance limits needed to determine whether the interval meets the study criterion.

General: bioequivalence is a conclusion tied to a specified statistical criterion and defined conditions. A ratio estimate alone, or a non-significant difference test, is not sufficient to establish that criterion. The record’s missing acceptance limits are important to interpretation. The numerical ratio and interval are available, but their status relative to the intended limits cannot be independently assessed from the registry record.

The result does not address clinical effectiveness, long-term use, repeated dosing, or outcomes outside the measured pharmacokinetic endpoint. It does not support conclusions about people with conditions other than the healthy-volunteer population, nor about dosing conditions other than the fed single-dose setting. The posted safety figures are likewise limited to the recorded adverse-event summaries. The interpretation should remain within the study’s measured endpoint and population.

17. Why This Trial Matters Statistically

This trial illustrates why the scale and purpose of an analysis matter. The posted arithmetic means and the unadjusted mean difference describe Cmax on its original measurement scale, while the sponsor’s bioequivalence analysis reports a geometric test-to-reference ratio. Both summaries concern the same endpoint, but they do not answer the same question. Treating the ratio and absolute difference as interchangeable would obscure the distinction between a proportional comparison and an absolute change.

It also demonstrates why failure to find a statistically significant difference is not equivalent to evidence of bioequivalence. The unadjusted p-value of 0.187 addresses a conventional difference question, whereas bioequivalence depends on whether a confidence interval for the relevant ratio satisfies prespecified limits. Those limits are not reported in the registry record. The ratio and interval are informative, but without the criterion they cannot be independently classified as meeting or failing the trial’s intended threshold.

The crossover design is another reason to distinguish posted summaries from a complete analysis. General: comparisons within the same participant can account for stable between-person variation, but an independent reconstruction requires information about paired observations and the model. The registry identifies ANOVA for the sponsor’s ratio analysis but does not report all model details. The arm-level means and standard deviations alone do not capture within-participant variability.

Finally, the study’s scope is narrow and clearly defined: healthy subjects, a fed setting, single doses, and a primary pharmacokinetic endpoint. This makes the results interpretable for that specific comparison while limiting what can be inferred beyond it. The record is useful for showing how distinct statistical summaries relate to a bioequivalence question and why reporting the criterion and analysis details is essential for transparent interpretation.

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.

The registry record does not report the bioequivalence acceptance limits. This prevents an independent assessment of whether the sponsor-reported 90% confidence interval satisfies the intended criterion, even though the geometric ratio and its interval are available. The record also does not provide full details of the ANOVA model, such as its terms or other implementation details. The sponsor analysis therefore cannot be completely reconstructed from the posted information.

The primary endpoint results list arm-level means, standard deviations, and analysis counts, but do not report the variability of within-participant differences. That information is particularly relevant to a crossover comparison. The registry also does not report the treatment sequences, washout interval, or a detailed account of the number and reasons for exclusions from the pharmacokinetic analysis. The stated exclusion for emesis within 12 hours is known, but the number of affected subjects is not reported in the registry record.

The record lists enrollment of 85, while the primary endpoint analysis counts are 79 and 81 and the safety group counts are 83 and 84. These figures reflect different reported parts of the record; the registry does not provide a complete participant-flow explanation that would reconcile them. No additional missing-data methods or sensitivity analyses are reported. The original sample-size justification and design assumptions are also not reported in the registry record; planning illustrations based on the observed effect do not fill that gap.

The study was open-label, single-center, and conducted in healthy subjects using single fed doses. Its results therefore have a limited setting and population. The posted record does not establish conclusions about repeated dosing, other populations, other conditions, or clinical outcomes beyond Cmax. These limitations describe the information and scope available in the record; they do not by themselves show that the study’s reported analysis was invalid.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: A Study to Determine the Fed Bioequivalence of Reformulated OXY Tablets and Original OxyContin® (OXY) Tablets — NCT01099709.
• Registry record last updated 2010-05-06; status last verified 2010-04.
• Results first posted 2010-05-06.
• 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

NCT01099709 is a completed Phase 1 randomized, open-label, single-center, single-dose, two-way crossover study in healthy subjects. It compared reformulated OXY 10 mg with original OxyContin® 10 mg in the fed state. The registry lists enrollment of 85 and identifies Cmax as the primary endpoint, measured in ng/mL over blood sampling lasting 72 hours.

The sponsor-reported geometric test-to-reference ratio multiplied by 100 was 105, with a 90% confidence interval from 101.06 to 108.51. The unadjusted recalculation of the arithmetic means gives a difference of 0.6 ng/mL, a 95% confidence interval from -0.291 to 1.491, and an unadjusted p-value of 0.187. The bioequivalence acceptance limits and full analysis specifications are not reported in the registry record, so the ratio cannot be independently judged against the intended criterion from the posted information alone.