An Efficacy and Safety Study of Acetaminophen Plus Tramadol Hydrochloride (JNS013) in Participants With Chronic Pain: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for An Efficacy and Safety Study of Acetaminophen Plus Tramadol Hydrochloride (JNS013) in Participants With Chronic Pain (NCT00736853), a randomized phase 3 study. The primary outcome is Number of Participants With Insufficient Pain Relief After the Start of Double-Blind Period.

2. Clinical Question

3. Trial Design

The registry describes a randomized, quadruple-masked, parallel-group Phase 3 study. The study enrolled 321 participants and is marked completed. Its recorded start was 2008-06, and its primary completion was 2009-01. These are registry dates, not a description of how long each participant was followed.

The intervention list includes an open-label period with tramadol hydrochloride plus acetaminophen, followed by a double-blind comparison of the combination with placebo. The primary endpoint timeframe is Day 28 of the double-blind period. The record does not give the length of the open-label period, the complete treatment schedule, or details of randomization and allocation concealment. Those details are not reported in the registry record.

The posted primary outcome is a count of participants classified as having insufficient pain relief. The efficacy analysis set is described as including participants who received at least one dose of study drug. The double-blind group counts are 94 for the combination and 93 for placebo. The enrollment figure of 321 refers to the study as a whole; the record does not explain the relationship between that figure and the smaller counts in the posted primary comparison.

The registry lists 23 outcome measures and posts results for 22 secondary outcomes. These include changes in VAS24, pain-intensity measures, pain-intensity difference, and pain relief during the open-label and double-blind periods. The record does not establish which outcomes were designated in the original protocol as primary or secondary beyond the posted primary outcome, nor does it report a full protocol or 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.

Open-Label Period

Reasons for not completing this period:

Double-Blind Period

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Efficacy analysis set included participants who received at least one dose of the study drug.

5. Baseline Characteristics

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

6. Primary Endpoint

The registry lists the primary outcome as Number of Participants With Insufficient Pain Relief After the Start of Double-Blind Period, measured over Day 28 of double-blind period.

The primary endpoint counts participants with insufficient pain relief after the start of the double-blind period, with the recorded timeframe ending at Day 28. The registry’s definition has two routes to classification. One is worsening of average pain intensity in daily living during the past 24 hours, measured using VAS24, on 2 consecutive days in the double-blind period compared with the average VAS24 during 3 days before the end of the open-label period. The other is a participant request to discontinue study drug because pain relief was insufficient.

This endpoint turns a pain experience and a participant’s decision to stop treatment into a count of participants meeting a defined event criterion. In general, a binary endpoint of this kind can be summarized as the number experiencing the event in each group and compared between groups. It is easier to interpret than a repeated series of pain scores, but it does not retain all the detail in the underlying pain measurements. Participants who meet the endpoint through worsening scores and those who request discontinuation are combined in the same count.

The posted primary counts were 20 in the combination group and 43 in the placebo group. The endpoint description does not report separate counts for its two criteria, nor does it give further detail about how missing pain assessments or discontinuations not attributed to insufficient relief were handled. Those details are not reported in the registry record.

7. Results Posted in the Registry

• Tramadol Hydrochloride and Acetaminophen (Double-Blind): 21.3% (20/94) versus 46.2% (43/93) on control; risk difference -25.0 percentage points (95% CI -38.0 to -11.9), risk ratio 0.46 (0.29–0.72); unadjusted two-proportion z-test p = <0.001.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary endpoint is binary: each participant is counted as either meeting the insufficient-pain-relief definition or not meeting it for the analysis. The registry posts an event count and group size for each double-blind arm. A simple unadjusted comparison estimates the event risk in each group from those counts and denominators, then expresses the contrast as a risk difference. A negative risk difference in the stated direction means that the event risk is estimated to be lower in the combination group than in the placebo group. The recalculation uses the posted summary statistics and does not adjust for other variables.

The recalculated test reports p < 0.001. In general, a p-value measures how unusual data at least as incompatible with a specified null model would be if that model were true, under the assumptions of the test. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of an effect. The registry reports one sponsor analysis using a log-rank method, but the record does not say whether its p-value or the recalculated p-value was designated as the primary inferential test in the original analysis plan.

The sponsor’s reported method is log-rank, with a hazard ratio as its effect measure. In general, the log-rank test compares event timing between groups over follow-up, while the hazard ratio describes the relative event hazard over time under the model’s interpretation. That is a different estimand from a fixed-time risk difference. A hazard ratio depends on event timing and on how participants without an observed event contribute to follow-up; it cannot be obtained from the two endpoint counts alone. The registry gives the sponsor’s hazard ratio and interval but does not report the event-time data, censoring approach, or additional model details.

The endpoint definition combines worsening VAS24 scores on consecutive days with a participant request to discontinue due to insufficient relief. In general, combining multiple qualifying events creates a single outcome that may be easier to analyze, but the combined estimate cannot show which component is driving the result. The record does not report component-specific results. It also does not explain how endpoint status was assigned for participants with incomplete VAS24 observations or discontinuations for other reasons.

Randomization supports a group comparison by allocating participants to study groups, but the registry’s summary does not report the randomization procedure, allocation concealment, or stratification factors. Quadruple masking is recorded, but the registry does not specify all roles covered by masking or the steps used to preserve it. The trial is described as parallel-group; that means the compared groups are separate rather than the same participants receiving both double-blind treatments in sequence. The record does not provide further operational detail.

The efficacy analysis set included participants who received at least one dose of study drug. This definition is not identical, on its face, to an analysis of every randomized participant. The registry does not give a participant flow diagram, numbers excluded from the efficacy set, or a full account of analysis populations. It also does not report an intention-to-treat definition, how protocol deviations were handled, or the approach to missing primary-outcome data.

Multiplicity concerns arise when several outcomes or comparisons are examined, because repeated testing can increase the chance of at least one apparently notable result under a null model. The registry lists 23 outcome measures and posts 22 secondary outcomes. This fact alone does not show how many formal hypotheses were tested, whether the outcomes were prespecified, or whether any adjustment was used. A multiplicity strategy is not reported in the registry record.

In general, over-dispersion matters when observed variability in a count outcome is greater than expected under a simple count model, because standard errors from that simpler model can be too small. The primary endpoint is posted as a participant count with a binary event definition, rather than a recurrent-event total per participant. The registry does not report an over-dispersion assessment or a model requiring that adjustment, so this concept should not be treated as a feature of the sponsor’s reported analysis.

Finally, the recalculated risk-difference comparison and the sponsor’s log-rank result answer related but not identical statistical questions. The recalculation is an unadjusted comparison based on the posted event counts and denominators. The sponsor’s analysis uses event timing. Neither can be fully reconstructed from the other, and the registry does not report enough analysis detail to independently reproduce the time-to-event result.

10. Confidence Intervals and Precision

A confidence interval describes a range of effect estimates compatible with the data and the method’s assumptions. In repeated use of the same method under the same conditions, intervals constructed in this way would cover the target parameter at the stated rate. A 95% confidence interval is not a statement that there is a 95% probability that the particular fixed parameter lies within the calculated interval.

For the sponsor’s hazard ratio, the posted estimate is 0.377 and the 95% confidence interval is 0.221 to 0.641. The interval lies below 1, the value corresponding to equal hazards. This indicates that the sponsor estimate is not especially close to the equality value across the interval’s range, under the reported method. The interval still allows a range of hazard-ratio magnitudes; it does not identify one exact effect size.

The unadjusted recalculation is based on the posted event counts and group sizes. It also has uncertainty, but the precision discussion should not substitute the sponsor’s time-to-event interval for an interval around the risk difference: they refer to different effect measures. The registry reports the sponsor interval, while the recalculated comparison is presented as a separate unadjusted analysis.

Precision is also limited by what the registry reports. The record does not give a detailed account of missing observations, event-time handling, or analysis-set flow, each of which can affect the interpretation of an estimate and its uncertainty. Confidence intervals quantify sampling uncertainty under a method; they do not account for every limitation in study conduct, outcome definition, or generalizability.

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 sample-size figures are planning illustrations based on the observed effect, not the trial’s original design assumptions. The registry record does not report the original sample-size justification or its assumptions. For this binary endpoint, the planning figures are participants per arm, not total events. The illustration assumes a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. It considers planning for the full observed effect, 75% of the observed effect, and 50% of the observed effect.

The 80% power column gives the number of participants per arm that the illustration estimates would be needed to have an 80% chance of detecting the specified effect, if the planning assumptions held and the effect were real. The 90% power column uses the same interpretation with a higher target chance of detection. These are design-planning quantities; they do not describe the probability that this completed trial’s result is correct.

The listed figures rise as the assumed effect becomes smaller: 56 participants per arm for 80% power and 74 for 90% power when planning for 100% of the observed effect; 104 and 138 when planning for 75%; and 241 and 322 when planning for 50%. Smaller effects need more participants to detect with the same target power, other assumptions being held constant. The curve should be read as a visual representation of this planning relationship, not as a record of the trial’s actual enrollment plan.

This is not observed power. It is a forward-looking illustration calculated from the observed effect under stated assumptions, and it should not be used to infer the trial’s original planning 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, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.462; treatment proportion p₁ = 0.213; average p̄ = 0.338.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6688 = 1.3107.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6450 = 0.5429.
4. n = (1.3107 + 0.5429)² / (-0.2496)² = 55.2, rounded up to 56 participants per arm for 80% power.

The smaller-effect rows in the table above repeat the same calculation with the effect multiplied by 0.75 and 0.5 (for ratios, applied to the logarithm of the ratio).

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
p0 <- 0.462365591397849                          # control proportion
p1 <- 0.212765957446809                          # treatment proportion
n_per_arm <- function(power, frac = 1) {
  q1 <- p0 + (p1 - p0) * frac               # smaller effect = fraction of the observed difference
  pbar <- (p0 + q1) / 2
  z_b <- qnorm(power)
  ceiling(round((z_a * sqrt(2 * pbar * (1 - pbar)) + z_b * sqrt(p0 * (1 - p0) + q1 * (1 - q1)))^2 / (q1 - p0)^2, 6))
}
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: n per arm = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(n_per_arm(0.80, f), big.mark = ","), format(n_per_arm(0.90, f), big.mark = ",")))

# Check against R's built-in function (unrounded n per arm)
cat("power.prop.test:", round(power.prop.test(p1 = p0, p2 = p1, power = 0.80)$n, 1), "\n")

# Simulation: how often does the z-test reject at the 80%-power sample size?
set.seed(736853)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 56 (80% power), 74 (90% power)
 75% of observed effect: n per arm = 104 (80% power), 138 (90% power)
 50% of observed effect: n per arm = 241 (80% power), 322 (90% power)
power.prop.test: 55.2 
Simulated power at n = 56 per arm: 0.815 (20000 replicates)

The simulation draws many pairs of event counts at the planned sample size and counts how often the two-proportion z-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

13. Analyses Reported by the Sponsor

The sponsor’s posted analysis uses the log-rank method and reports a hazard ratio of 0.377, with a 95% confidence interval from 0.221 to 0.641. The registry also posts the primary endpoint counts by double-blind group. The recalculated comparison uses those counts and group sizes to estimate an unadjusted risk difference and test, rather than reproducing the sponsor’s time-to-event analysis.

These analyses are related but not interchangeable. The recalculation treats the outcome as a binary event classification for the posted endpoint, whereas the log-rank method uses event timing. Differences in estimand and analysis method mean that the two results should not be expected to be numerically identical. The registry does not provide sufficient event-time or censoring detail to rebuild the sponsor’s estimate from the summary counts.

No discrepancy is flagged between the posted data and the recalculated summary-statistic comparison. The sponsor’s analysis remains the analysis reported by the registry, while the recalculation is a separate, simple unadjusted check using the posted counts. The original statistical analysis plan and the sponsor’s complete analysis details are not reported in the registry record.

14. Multiplicity, Missing Data and Analysis Populations

The registry lists 23 outcome measures and posts 22 secondary outcomes. The secondary outcomes cover pain scores and changes in VAS24, pain intensity, pain-intensity difference, and pain relief during the open-label and double-blind periods. The presence of several outcomes makes multiplicity a relevant interpretive consideration, but the registry listing does not establish how many outcomes were formally tested or which were prespecified for confirmatory inference.

The multiplicity strategy is not reported in the registry record. It is therefore not possible to determine from this record whether the analyses used a family-wise error adjustment, a hierarchical testing plan, or another approach. The unadjusted recalculation should be read as an unadjusted result, not as evidence that the original sponsor analysis did or did not account for multiple comparisons.

The efficacy analysis set is described as participants who received at least one dose of study drug. The registry does not report a complete account of randomized participants, exclusions, protocol deviations, or the number of participants included in each analysis beyond the posted group counts. It does not state whether the sponsor also conducted an intention-to-treat analysis or other sensitivity analyses.

Missing-data methods are not reported in the registry record. This matters because the primary endpoint definition includes repeated VAS24 assessments and a participant request to discontinue due to insufficient relief. The record does not explain how incomplete assessments, withdrawal for other reasons, or participants without endpoint classification were handled. It also does not report imputation methods or sensitivity analyses for missing outcomes.

These omissions do not establish that the study failed to address multiplicity or missingness in its full analysis. They limit what can be concluded from the registry record alone about those aspects of the statistical plan and the robustness of the results.

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 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: rectal cancer (1.1%).

The registry posts serious adverse event figures separately for the open-label and double-blind groups. In the open-label combination group, 0 serious adverse events were recorded among 277 participants at risk. In the double-blind combination group, 1 was recorded among 94 participants at risk. In the placebo group, 0 were recorded among 93 participants at risk. These are counts as posted, not adjusted comparisons.

The record lists rectal cancer at 1.1% among the top serious-event terms. It does not provide a detailed account in this summary of the event’s timing, outcome, or relationship to study treatment. Serious adverse events are not necessarily caused by the study drug; the registry counts alone do not establish causality.

The record also posts participants affected by other adverse events: 222 in the open-label group, 47 in the double-blind combination group, and 44 in the placebo group. These figures concern a different adverse-event category from serious events and should not be conflated. Deaths are not reported in the registry record. The posted safety information does not provide the detail needed to compare event types, duration, severity, or treatment attribution comprehensively.

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

The primary endpoint records insufficient pain relief using a defined combination of worsening VAS24 scores or a request to discontinue study drug for insufficient relief. The posted double-blind counts are 20 of 94 for tramadol hydrochloride plus acetaminophen and 43 of 93 for placebo. The sponsor’s time-to-event analysis reports a hazard ratio of 0.377, with a 95% confidence interval from 0.221 to 0.641. These are the results of this study as recorded in the registry.

Those results do not by themselves explain whether the endpoint difference arose mainly from worsening VAS24 scores, discontinuation requests, or both; separate component counts are not reported. Nor do they provide condition-specific estimates for participants with knee osteoarthritis versus low back pain. The findings should therefore not be assumed to describe each condition identically.

The endpoint is a defined trial outcome, not a complete description of pain experience, function, or every outcome important to participants. The registry lists additional pain-related outcomes, but the primary comparison alone does not convey all of them. The serious adverse-event figures are also limited summaries and do not establish whether any event was caused by treatment or capture the full benefit-harm balance.

General statistical interpretation also requires separating evidence against an equality model from the size and importance of an effect. A small p-value does not measure clinical importance, and a confidence interval does not resolve limitations such as missing analysis details or uncertain generalizability. The registry record does not provide a threshold for clinically important change in the primary endpoint.

Accordingly, the result describes the recorded comparison and its statistical precision, rather than offering treatment advice or a conclusion that applies to every person with chronic pain. Interpretation beyond this trial requires attention to the population, endpoint definition, analysis methods, safety information, and the limitations of the available registry entries.

17. Why This Trial Matters Statistically

This study illustrates why the endpoint definition matters as much as the name of an outcome. “Insufficient pain relief” is not a single direct measurement: the registry combines a specified worsening in VAS24 with a participant-requested discontinuation due to insufficient relief. A single count makes the comparison readable, but it conceals how often each route to the endpoint occurred and whether the routes behaved similarly.

It also demonstrates that different statistical methods can describe related aspects of an outcome without estimating the same quantity. The posted counts support a binary comparison at the endpoint, while the sponsor’s log-rank analysis uses event timing and reports a hazard ratio. A sound reading keeps those estimands separate rather than treating the hazard ratio as a restatement of the event-count difference.

The trial record also makes the distinction between an observed result and a planning illustration important. The sample-size figures are based on the observed effect and stated planning assumptions. They are not a reconstruction of the original design rationale, which is not reported in the registry record, and they do not measure the trial’s observed power.

Finally, the record shows how uncertainty in registry reporting shapes interpretation. The endpoint counts and sponsor estimate are available, but details on missing data, multiplicity, event-time handling, and condition-specific outcomes are not. Statistical conclusions are strongest when the estimate is considered alongside the design and the limits of the recorded analysis, not in isolation.

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 describes a population with chronic pain associated with knee osteoarthritis or low back pain, but does not report the numbers in each condition or separate treatment estimates. The extent to which the posted result applies similarly to both conditions cannot be assessed from this record. The brief summary also describes pain that could not be controlled sufficiently with non-steroidal anti-inflammatory drugs, so the study population should not be assumed to represent all people with chronic pain.

The primary endpoint combines worsening VAS24 measurements and participant-initiated discontinuation due to insufficient relief. The registry does not provide component-specific counts, so it is not possible to distinguish the contribution of these criteria. It also does not explain how missing repeated pain assessments or discontinuations for other reasons were treated.

The study includes an open-label period followed by a double-blind period, but the registry does not give the open-label duration, detailed transition rules, or the full randomization and allocation procedures. The primary comparison has group counts of 94 and 93, while overall enrollment is 321; participant flow explaining these figures is not reported in the registry record.

The sponsor’s log-rank analysis is reported with a hazard ratio and confidence interval, but event-time definitions, censoring rules, and full analysis details are not included. Multiplicity handling, the original sample-size justification, and the complete missing-data strategy are also not reported. These omissions restrict independent assessment of the analysis plan and its sensitivity to assumptions.

Safety reporting is summarized as counts, without full event narratives or a detailed account of attribution and timing. The available serious-event information should not be treated as a complete characterization of safety. These limitations concern the information in the registry record and do not establish what may have been reported elsewhere.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: An Efficacy and Safety Study of Acetaminophen Plus Tramadol Hydrochloride (JNS013) in Participants With Chronic Pain — NCT00736853.
• Registry record last updated 2013-09-26; status last verified 2013-07.
• Results first posted 2013-09-26.
• 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

NCT00736853 is a completed randomized, quadruple-masked, parallel-group Phase 3 study sponsored by Janssen Pharmaceutical K.K. It enrolled 321 participants and evaluated tramadol hydrochloride plus acetaminophen during a double-blind period against placebo in participants with chronic pain associated with knee osteoarthritis or low back pain.

The primary endpoint was the number of participants with insufficient pain relief by Day 28 of the double-blind period. The posted counts were 20 of 94 in the combination group and 43 of 93 in the placebo group. The sponsor reported a log-rank hazard ratio of 0.377, with a 95% confidence interval from 0.221 to 0.641. The registry also lists secondary pain outcomes and summarizes adverse events. Detailed information about multiplicity, missing-data handling, and the original sample-size rationale is not reported in the registry record.