A Study to Evaluate Efficacy and Safety of Oxycodone/Naloxone Compared to OxyContin in Korean Cancer Patients: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study to Evaluate Efficacy and Safety of Oxycodone/Naloxone Compared to OxyContin in Korean Cancer Patients (NCT01313780), a randomized phase 4 study. The primary outcome is Change of Pain Intensity From Baseline(visit1) to 4weeks.(visit3).

2. Clinical Question

Pain intensity was recorded on a 0-to-10 scale, with 0 described as no pain and 10 as the worst pain imaginable. The primary measure was the change from baseline to the four-week visit. The brief summary describes average pain over 24 hours, obtained each evening, as the measure used for the primary objective. The posted group results give mean changes of 1.586 for oxycodone/naloxone and 1.559 for oxycodone. The reported mean difference, comparing oxycodone with oxycodone/naloxone, is -0.027.

This is a question about a group-level outcome over a defined period. It does not establish how any individual participant's pain changed, and the registry results do not provide individual observations or a detailed distribution of responses. The record lists bowel habit as a secondary outcome; its brief summary also names rescue medication, quality of life, laxative use, and adverse events as secondary objectives. Detailed results for those objectives are not all present in the posted results. The statistical interpretation therefore centers on the primary pain measure and its uncertainty, not on unreported outcomes or a broader claim about treatment effects.

3. Trial Design

The record describes a randomized, multicentre, open-label, parallel-group, active-control Phase IV study. Its official title specifies a four-week study in Korean patients with cancer pain. Participants were assigned to oxycodone/naloxone or oxycodone alone. The registry lists enrollment as 128 and study status as completed. The start is recorded as 2011-05 and primary completion as 2013-10. These dates describe the registry entry; they do not provide a detailed account of recruitment, follow-up, or the timing of individual assessments.

Random allocation can help balance groups at the start of a study, on average, but the registry record does not report how the random sequence was generated, whether allocation was concealed, or whether any stratification was used. The study was unmasked. Participants and study personnel therefore knew which treatment was assigned, although the record does not describe how this might have affected outcome assessment or other study procedures. The parallel-group model means the recorded comparison is between groups assigned to different treatments, rather than a within-person crossover.

The primary outcome is the mean change in pain intensity from baseline to four weeks. The results identify an analysis population described as FAS: 117. The registry record does not define that population or explain how it differs from participants enrolled or assigned to treatment. Arm-level primary results list 58 participants for oxycodone/naloxone and 59 for oxycodone. Those result counts should not be treated as a complete account of all participants enrolled, randomized, treated, or followed, because the record does not give a participant-flow description.

The brief summary names bowel habit, rescue medication use, quality of life, time to laxative use, and adverse events among the secondary objectives. The registry record lists one secondary outcome as posted. It does not provide detailed results for all outcomes named in the brief summary. The original protocol, the study's own sample-size justification, and its full statistical analysis plan 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

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Analysis of FAS: 117.

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 Change of Pain Intensity From Baseline(visit1) to 4weeks.(visit3), measured over 4weeks.

The primary endpoint measures the change in pain intensity from baseline to the four-week visit. Pain is described on a scale from 0, meaning no pain, to 10, meaning the worst pain imaginable. The brief summary says average pain over 24 hours was obtained each evening. A change score condenses measurements over the treatment period into a comparison of the recorded starting and later values, while the group mean summarizes those changes across participants.

This kind of continuous outcome is useful for comparing groups because it retains information across the scale, rather than reducing each participant's report to a simple category. The mean describes the average recorded change, while the standard deviation describes how much participant-level values vary around that average. The registry reports means of 1.586 and 1.559, with standard deviations of 2.217 and 2.215 for the two groups. The group means are close, but the standard deviations indicate substantial variation relative to the reported mean difference.

The endpoint alone does not explain the direction or clinical importance of a change unless the scoring and subtraction convention are clear. The registry describes the measure and its scale but does not explicitly state whether the change was calculated as follow-up minus baseline or baseline minus follow-up. The results should therefore be read as recorded mean change scores and a between-group contrast, without assigning an unreported direction of improvement. The registry also does not report a threshold defining a clinically important difference. A statistically estimated difference and a judgment about clinical importance are related but distinct questions.

7. Results Posted in the Registry

• Oxycodone: mean 1.56 versus 1.59 on control; difference -0.03 (95% CI -0.83 to 0.78), standardized effect d = -0.01; z-test p = 0.947.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary outcome is continuous: each participant contributes a pain change score, and the registry summarizes those scores with a mean and standard deviation. The mean is the arithmetic average of recorded values. The standard deviation describes their dispersion around the mean. These summaries help characterize the group results, but they do not show the shape of the underlying distribution or whether a small number of observations had unusual influence.

What does the mean difference represent?

The reported contrast is oxycodone minus oxycodone/naloxone. Its estimate is -0.027, based on arm means of 1.559 and 1.586, respectively. A difference near zero means the average recorded change scores were similar in this sample. The sign depends on the stated comparison order; it should not be interpreted as improvement or worsening without a clear change-score convention. The registry record does not explicitly state that convention.

A between-group contrast is distinct from the within-group change in either arm. The values are reported as group mean changes from baseline, whereas the comparison asks how those changes differed between assigned groups. Neither the contrast nor the p-value describes how many participants improved, how many worsened, or the experience of a typical individual. Those details are not reported in the registry record.

How should the confidence interval be read?

The 95% confidence interval runs from -0.830 to 0.776 after rounding to three decimal places. In general, a confidence interval is a range of values compatible with the data under the statistical model used to estimate it. It conveys precision as well as direction: a narrow range indicates a more precise estimate, while a wider range leaves greater uncertainty. The interval includes zero and extends on both sides of it. Thus the posted result does not pinpoint a nonzero difference, but it also does not restrict plausible differences to values extremely close to zero.

Confidence intervals do not assign a probability to a particular fixed treatment effect after the data have been observed. Nor do they determine clinical importance on their own. To assess whether the interval is compatible with non-inferiority, it would need to be compared with a prespecified margin and interpreted in light of the designated analysis. Those details are not reported in the registry record.

What does the p-value add?

The unadjusted p-value is 0.947. In general, a p-value measures how compatible the observed data are with a specified null hypothesis, assuming the model and its assumptions. It is not the probability that the null hypothesis is true, and it does not measure the chance that the result is due to chance. A large p-value is not evidence of equivalence, because a conventional test for a difference and a non-inferiority test answer different questions. The registry record does not report a formal non-inferiority test or its margin.

The posted estimate and uncertainty can be understood without treating the p-value as a verdict. The estimate gives the observed contrast, the interval describes a range of compatible values, and the p-value summarizes a test against a null of no difference. Each answers a different part of the statistical question. For a non-inferiority objective, the prespecified margin and confidence-interval decision rule are essential.

Why does variability matter?

The two standard deviations are 2.217 and 2.215, while the mean difference is -0.027. In general, larger variability makes a group contrast harder to estimate precisely if other design features are unchanged. It can make the confidence interval wider, because observed outcomes scatter more around their group averages. This does not mean variability is a defect in the data: it may reflect genuine differences among participants, measurement noise, or other influences. The registry record does not separate those possible sources.

These summaries also do not establish that a normal model was used for the trial's original analysis. The planning illustration describes a normal approximation, but the trial's own statistical methods are not reported in the registry record. The planning assumption should not be mistaken for evidence about the actual analysis. The record does not give diagnostic checks, adjusted models, or sensitivity analyses.

What can be concluded about the analysis population?

The primary result is described as an analysis of FAS, with 117 participants. The arm results list 58 and 59 participants. The registry record does not define FAS, state the exact inclusion rules, or explain how missing endpoint values were handled. It also does not report a per-protocol result. These details matter for non-inferiority interpretation because exclusions and missing outcomes can affect the estimated contrast. Without the analysis-population definition and missing-data approach, the posted estimate can be described, but its robustness to alternative analysis choices cannot be evaluated.

Likewise, the registry record does not report whether the analysis adjusted for baseline pain, site, or other variables; whether any interim analyses were planned or conducted; or what multiplicity procedure was used. Those methods should not be inferred from the study's randomized design or from the planning assumptions. The posted summary supports a description of the observed mean contrast and its unadjusted precision, while important details of the trial's own statistical plan remain unreported.

10. Confidence Intervals and Precision

The mean difference is -0.027, with a 95% confidence interval from -0.830 to 0.776 when expressed to three decimal places. This interval is broad relative to the point estimate: it includes zero and allows for differences in either direction. The estimate therefore has limited precision for distinguishing a small difference from no difference. The interval's endpoints are rounded to three decimal places to follow the reporting precision limit.

In general, a confidence interval reflects both the amount of information in the data and the variability of the outcome, under the method used to calculate it. The reported standard deviations are 2.217 and 2.215, while the arm-level results include 58 and 59 participants. The record does not report a confidence interval for each arm mean, nor does it specify the trial's original interval-estimation method. The interval for the contrast is the most direct summary of uncertainty about the between-group result.

Precision is not the same as statistical significance or clinical importance. The interval includes zero, but that alone does not prove equivalence. Whether its limits rule out an unacceptable difference for the non-inferiority objective depends on a prespecified margin. The margin is not reported in the registry record, and the study's formal decision rule is also not reported. There is therefore no basis in the registry record to classify the interval as meeting or failing the intended non-inferiority criterion.

The interval also does not indicate the probability that the true difference lies between its limits. In general, it is a range generated by a method with a stated long-run coverage property under its assumptions. Its practical meaning depends on whether those assumptions and the analysis population are appropriate. Since the record does not describe missing-data handling, model checks, or adjusted analyses, the robustness of the interval cannot be assessed from the posted summary alone.

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 participants and not total events. They illustrate the sample size that a hypothetical study might require under the assumptions stated for the planning calculation. The effect to detect is set at the observed effect, or at a stated fraction of that observed effect. The smaller-effect scenarios therefore represent targets closer to no difference than the observed contrast.

The calculation assumes a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The trial's own original design assumptions and sample-size justification are not reported in the registry record. These planning figures are not observed power: they are planning illustrations based on the observed effect, not a measure of the study's realized probability of detecting an effect.

The 80% power column describes the number of participants per arm required, under those assumptions, for a hypothetical study to have an 80% probability of detecting the specified effect at the stated significance level if that effect were the true one. The 90% power column uses a higher target probability and therefore gives a larger planning requirement for the same effect. These are prospective design concepts, not properties established by the completed trial's result.

For the full observed effect, the figures are 105,742 participants per arm for 80% power and 141,559 participants per arm for 90% power. Planning for 75% of the observed effect gives 187,986 and 251,659 participants per arm, respectively. Planning for 50% of the observed effect gives 422,967 and 566,233 participants per arm, respectively. Smaller effects require more participants because they are harder to distinguish from the variability in the outcome. These very large illustrations also reflect that the observed mean difference is close to zero; they should not be read as recommendations for this clinical question or as the original trial's planned enrollment.

The record describes the trial as enrolling 128. That actual enrollment is distinct from the hypothetical per-arm planning figures, and the planning figures should not be used to infer what the investigators intended when designing the study. No event-based sample-size interpretation applies to this continuous primary outcome.

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 = -0.027; pooled standard deviation σ = 2.216.
2. n = 2 × (1.96 + 0.842)² × 2.216² / -0.027² = 105,741.7, rounded up to 105,742 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 <- -0.0270000000000001                      # observed difference in means
sigma <- 2.21599152996341                     # 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(1313780)
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 = 105,742 (80% power), 141,559 (90% power)
 75% of observed effect: n per arm = 187,986 (80% power), 251,659 (90% power)
 50% of observed effect: n per arm = 422,967 (80% power), 566,233 (90% power)
power.t.test: 105742.7 
Simulated power at n = 105,742 per arm: 0.803 (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. Multiplicity, Missing Data and Analysis Populations

The record identifies pain change as the primary outcome and lists change in bowel habits as one secondary outcome. The brief summary names additional secondary objectives, including rescue medication, quality of life, duration to laxative use, and adverse events. Detailed results for all those objectives are not present in the registry record. The record lists one secondary outcome as posted and no analysis entries. It does not describe a hierarchy of tests or a procedure for controlling the chance of false-positive findings across multiple outcomes.

In general, multiplicity matters when several outcomes or comparisons are tested: the more opportunities to find a statistically notable result, the greater the chance of at least one such result by chance if no adjustment or prespecified hierarchy is used. The registry record does not report whether such a method was planned or applied. The posted primary p-value is described as unadjusted, so it should not be interpreted as evidence that multiplicity was controlled.

The record names the primary analysis population as FAS and gives 117 as its size, but it does not define the population or specify how participants were included. The arm-level result counts are 58 and 59. It does not provide a flow of participants through assignment, treatment, follow-up, and analysis, or explain any differences between those stages. The handling of missing baseline or four-week pain measurements is not reported in the registry record.

In general, missing outcomes can influence a group comparison, especially if missingness differs between groups or is related to the unobserved outcome. Common approaches include explicit assumptions about missing values and sensitivity analyses under alternative assumptions, but no such approach should be attributed to this study without documentation. The registry record does not report imputation, a complete-case rule, or sensitivity analyses.

These gaps are particularly relevant to a non-inferiority question. Excluding participants or handling missing outcomes in a way that makes groups appear more alike can affect interpretation. This is a general methodological concern, not evidence that it occurred in this trial. With the analysis-population definition, missing-data method, and non-inferiority margin unreported, the posted summary cannot establish the robustness of a non-inferiority conclusion.

14. 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 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: pneumonia (3.1%), glucose, serum-low (hypoglycemia) (3.1%), pain (3.1%), anaphylactic shock (1.6%), leukocytosis (1.6%).

The safety results distinguish serious adverse events from other adverse events. In the oxycodone/naloxone group, 15 of 64 participants at risk were reported with a serious adverse event, and 55 of 64 with another adverse event. In the oxycodone group, the corresponding figures were 28 of 64 and 57 of 64. These are participant counts as recorded, not rates calculated for a different follow-up period. The registry does not report exposure-adjusted rates or the time at risk for individual participants.

The serious-event terms listed include pneumonia, glucose, serum-low (hypoglycemia), and pain, each at 3.1%, and anaphylactic shock, leukocytosis, and neutropenia, each at 1.6%. The registry record does not identify arm-specific counts for these listed terms in the information, so they should not be assigned to one treatment group. The terms are not a substitute for a full event listing or an assessment of causal relationship.

Deaths are not reported in the registry record. The counts alone do not establish whether an event was caused by treatment, and differences in counts should not be treated as proof of a treatment effect. The record does not provide detailed information about event definitions, timing, severity beyond serious versus other, or exposure duration by group.

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

The posted primary result describes similar group mean change scores at four weeks: 1.586 for oxycodone/naloxone and 1.559 for oxycodone. The between-group estimate is -0.027, and the unadjusted 95% confidence interval ranges from -0.830 to 0.776. These data place the point estimate close to zero, but the interval leaves room for differences in either direction. The result is therefore best read as an uncertain estimate of the average contrast, not as proof that the treatments have identical effects.

The study's stated objective was non-inferiority. A conclusion on that objective requires an agreed margin describing how much worse a treatment could be and still meet the criterion, as well as a suitable analysis and decision rule. The margin and formal analysis are not reported in the registry record. The p-value of 0.947 is an unadjusted test result and does not, by itself, answer the non-inferiority question. It also cannot establish equivalence.

The outcome is a group mean change on a pain scale, not a summary of every participant's experience. The reported standard deviations indicate variation in the recorded change scores. The registry record does not show the distribution of individual responses, the proportion with improvement or worsening, or a threshold for clinical importance. It does not specify the direction convention for calculating change, so the means should not be labeled as improvement or worsening without that information.

The result applies to the recorded four-week assessment and the described FAS population. It does not determine longer-term outcomes, effects in other populations, or the results of secondary objectives for which detailed findings are not posted. The safety counts are a separate part of the record and do not resolve the primary efficacy uncertainty. Taken together, the registry results support a narrow statement about the observed average contrast and its imprecision, while leaving the intended non-inferiority conclusion and broader clinical meaning unresolved.

16. Why This Trial Matters Statistically

This trial illustrates why a small estimated difference and a non-significant p-value are not enough to establish non-inferiority. The observed mean contrast is close to zero, and the unadjusted p-value is 0.947. Yet the confidence interval spans values on both sides of zero, and the record does not report the margin needed to judge whether the interval excludes an unacceptable difference. The statistical question depends on both the estimate and the prespecified decision threshold.

It also shows why precision matters alongside the point estimate. The standard deviations are 2.217 and 2.215, whereas the estimated between-group difference is -0.027. Individual-level variation is substantial relative to the group contrast, and the interval remains compatible with a range of effects. Similar group averages are not the same as evidence that a clinically relevant difference has been ruled out.

The study's randomized, parallel-group, active-control design is suited to a direct comparison, but the registry summary does not report key details needed to assess the intended claim. The non-inferiority margin, analysis rules, missing-data handling, and definition of FAS are not reported. Those details are central to a transparent interpretation, especially when the conclusion is framed as non-inferiority rather than superiority.

Finally, the record separates the primary pain outcome from a broader set of secondary objectives and safety observations. Detailed results for all listed secondary objectives are not posted. This is a useful reminder that a trial's stated questions and its available results are not always equally detailed in a registry record. Statistical conclusions should stay within the outcome, time point, and analysis information that is actually documented.

17. Limitations

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

The registry record leaves several trial-specific uncertainties. It states that assignment was randomized and that the study was open-label, but does not report the sequence-generation method, allocation concealment, or any blinding of outcome assessment. Knowledge of treatment assignment could be relevant to a participant-reported pain outcome, although the record does not document whether or how it affected assessments. The extent of this concern cannot be quantified from the posted information.

The primary result is described as coming from FAS, but the record does not define that population. Although the arm results list 58 and 59 participants and the primary outcome description gives 117 for FAS, the record does not provide a participant flow or explain who was excluded from each analysis. The missing-data approach for the four-week endpoint is also not reported. These omissions prevent assessment of whether the result is sensitive to inclusion rules or unavailable observations.

The non-inferiority margin, the original sample-size justification, and the trial's own statistical analysis plan are not reported. The planning figures are illustrations based on the observed effect and should not be taken as the original design calculation. The registry record also does not report interim analyses, adjustment for baseline variables, model diagnostics, or sensitivity analyses. None of these methods can be presumed from the study's design label.

The endpoint description does not make the arithmetic convention for change explicit, and no threshold for a clinically important difference is reported. The result is limited to a four-week mean pain change. Detailed findings for several secondary objectives named in the brief summary are not included, and the serious adverse-event terms are not allocated to treatment arms in the listed information. These limitations constrain interpretation of both the intended non-inferiority question and the broader balance of outcomes.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: A Study to Evaluate Efficacy and Safety of Oxycodone/Naloxone Compared to OxyContin in Korean Cancer Patients — NCT01313780.
• Registry record last updated 2017-12-22; status last verified 2017-11.
• Results first posted 2016-10-27.
• 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.

21. Record Summary

The registry record describes a completed, randomized, open-label, parallel-group, active-control Phase IV study of oxycodone/naloxone compared with oxycodone alone in Korean patients with cancer pain. The official title specifies a four-week study. The primary endpoint is mean change in pain intensity from baseline to four weeks on a 0-to-10 scale.

The reported group means are 1.586 and 1.559, with a mean difference of -0.027 for oxycodone compared with oxycodone/naloxone. The unadjusted 95% confidence interval is -0.830 to 0.776 when rounded to three decimal places, and the unadjusted p-value is 0.947. The estimate is close to zero, but its uncertainty does not establish equivalence or resolve the stated non-inferiority objective.

The registry record does not report the non-inferiority margin, the original sample-size justification, the detailed analysis plan, or the handling of missing endpoint data. It lists adverse-event counts and one secondary outcome, but does not give detailed results for every objective named in the brief summary.