Tapentadol IR vs Oxycodone IR vs Placebo in Acute Pain From Vertebral Compression Fracture Associated With Osteoporosis: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Tapentadol IR vs Oxycodone IR vs Placebo in Acute Pain From Vertebral Compression Fracture Associated With Osteoporosis (NCT00771758), a randomized phase 3 study. The primary outcome is Sum of Pain Intensity Difference Over 3 Days (SPID72).

2. Clinical Question

The clinical question concerns the pattern of reported pain scores during a short treatment period, rather than a long-term outcome. The active-treatment comparisons are each against placebo; the posted results do not report a direct statistical comparison between tapentadol IR and oxycodone IR. The registry’s primary outcome description defines the analysis population and the direction of the score, which are important when interpreting the numerical comparisons.

3. Trial Design

The registry describes a randomized, quadruple-masked, parallel-group phase 3 study of tapentadol IR, oxycodone IR, and placebo. It lists 108 enrolled participants and reports that the study was completed after being terminated prematurely because of slow enrollment, after 108 of 600 planned subjects had enrolled. The registry record does not report the trial’s original sample-size assumptions or the rationale for the planned enrollment.

The three groups received capsules on an as-needed schedule for up to 10 days. Tapentadol IR was given as 50 or 75 mg capsules, with a maximum daily dose of 450 mg. Oxycodone IR was given as 5 or 10 mg capsules, with a maximum daily dose of 60 mg. The placebo group received one capsule on the same as-needed interval. These descriptions establish the assigned regimens; they do not establish how much medication participants actually took.

The primary endpoint was SPID72, the time-weighted sum of pain-intensity differences over 72 hours. The registry defines the modified Intent-to-Treat population as randomized participants who took at least one dose and had a qualifying baseline pain assessment through the Interactive Voice Response system. The outcome arm counts are 36.0 for tapentadol IR, 41.0 for oxycodone IR, and 20.0 for placebo. The endpoint results therefore concern this reported analysis population, not necessarily every person enrolled.

The registry lists 45 outcome measures and 0 analyses. It includes secondary pain-responder outcomes and other SPID windows, but the registry record does not report a detailed statistical analysis plan, the trial’s original power assumptions, or methods for handling missing outcome data. The stated reason for early termination was slow enrollment.

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: The study consisted of a screening/randomization period (one day) and a double blind active treatment period (10 days).

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The modified Intent-to-Treat(mITT) population was defined as all randomized patients who took at least one dose of study drug and had a baseline pain intensity assessment via the Interactive Voice Response (IVR) system with score ≥5 on an 11-point NRS.

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 Sum of Pain Intensity Difference Over 3 Days (SPID72), measured over 3 Days (72 hours).

The primary endpoint, Sum of Pain Intensity Difference Over 3 Days (SPID72), summarizes pain-intensity changes during the first 72 hours. Pain intensity was assessed on an 11-point numerical rating scale, from 0 for no pain to 10 for pain as bad as you can imagine. At each assessment, pain-intensity difference was calculated as baseline pain intensity, measured before the first dose, minus current pain intensity. SPID72 is the time-weighted sum of those differences over 72 hours.

The endpoint can range from -720 to 720, and a higher value indicates greater pain relief. Because it combines pain-intensity differences across time, it represents the overall pattern during the assessment window rather than a single pain score at one moment. The time weighting also means that the timing and availability of assessments matter to the result. The registry record does not report details of the weighting algorithm beyond describing SPID72 as a time-weighted sum.

Using a continuous endpoint retains distinctions in the magnitude of participants’ scores rather than reducing the outcome to whether a person did or did not cross a responder threshold. That can make it useful for describing average change over a defined period. However, a group mean does not show the full distribution of individual experiences, and the registry does not report a clinical threshold for interpreting a particular difference in SPID72. The outcome should therefore be read alongside its uncertainty and the registry’s explicit caution about the low enrollment.

7. Results Posted in the Registry

• Tapentadol IR: mean 139.00 versus 114.20 on control; difference 24.80 (95% CI -36.77 to 86.37), standardized effect d = 0.20; z-test p = 0.430.
• Oxycodone IR: mean 129.40 versus 114.20 on control; difference 15.20 (95% CI -41.11 to 71.51), standardized effect d = 0.14; z-test p = 0.597.

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.

30% Responder Rate on Day 3.

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Tapentadol IR: 36.1% (13/36) versus 50.0% (10/20) on control; risk difference -13.9 percentage points (95% CI -40.8 to 13.1), risk ratio 0.72 (0.39–1.34); unadjusted two-proportion z-test p = 0.311.
  • Oxycodone IR: 39.0% (16/41) versus 50.0% (10/20) on control; risk difference -11.0 percentage points (95% CI -37.5 to 15.5), risk ratio 0.78 (0.44–1.40); unadjusted two-proportion z-test p = 0.416.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Tapentadol IR and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Oxycodone IR and the control. The interval gives the range of effects that remain compatible with the data.

50% Responder Rate on Day 3.

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Tapentadol IR: 25.0% (9/36) versus 25.0% (5/20) on control; risk difference 0.0 percentage points (95% CI -23.7 to 23.7), risk ratio 1.00 (0.39–2.58); unadjusted two-proportion z-test p = 1.000.
  • Oxycodone IR: 24.4% (10/41) versus 25.0% (5/20) on control; risk difference -0.6 percentage points (95% CI -23.7 to 22.5), risk ratio 0.98 (0.38–2.48); unadjusted two-proportion z-test p = 0.959.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Tapentadol IR and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Oxycodone IR and the control. The interval gives the range of effects that remain compatible with the data.

30% Responder Rate on Day 5.

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Tapentadol IR: 44.4% (16/36) versus 35.0% (7/20) on control; risk difference 9.4 percentage points (95% CI -17.0 to 35.9), risk ratio 1.27 (0.63–2.56); unadjusted two-proportion z-test p = 0.491.
  • Oxycodone IR: 48.8% (20/41) versus 35.0% (7/20) on control; risk difference 13.8 percentage points (95% CI -12.1 to 39.7), risk ratio 1.39 (0.71–2.74); unadjusted two-proportion z-test p = 0.309.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Tapentadol IR and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Oxycodone IR and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary outcomes cover responder thresholds at several assessment days and SPID windows shorter or longer than the primary 72-hour measure. Across these measures, the pattern is not consistently in the same direction: some observed responder percentages are higher in an active-treatment group than in placebo, while others are similar or lower. The small outcome groups and broad uncertainty in the comparisons make the pattern unstable rather than a clear, consistent separation across outcomes.

These outcomes add context to the primary result by asking related questions in different ways: responder thresholds classify participants according to a specified degree of improvement, while SPID summarizes pain-intensity differences over time. Agreement across related measures might strengthen a coherent interpretation, but the posted secondary results do not remove the uncertainty of the primary comparisons. Nor should isolated numerical differences be treated as proof of an effect when the primary analysis itself is imprecise and the study was stopped early.

Unadjusted secondary comparisons carry less weight because multiple outcomes create multiple opportunities for chance findings. Without a reported multiplicity procedure or prespecified hierarchy, the registry record does not establish which secondary outcomes were intended to be confirmatory. The registry lists 45 outcome measures, and 44 secondary outcomes are posted; the record reports 0 analyses. These details support caution in interpreting secondary results as a group. They are best viewed as descriptive or exploratory evidence that may inform questions for future research, not as a set of independent confirmations.

The registry record does not report a complete analysis plan, how missing secondary measurements were handled, or a sponsor-reported inferential analysis for these outcomes. Those gaps limit how confidently the secondary pattern can be compared across assessment times and thresholds. The secondary findings should therefore be read in light of the trial’s low enrollment and the registry’s warning that valid statistical conclusions cannot be made.

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

• 30% Responder Rate on Day 3.
• 50% Responder Rate on Day 3.
• 30% Responder Rate on Day 5.
• 50% Responder Rate on Day 5.
• 30% Responder Rate on Day 10.
• 50% Responder Rate on Day 10.
• Sum of Pain Intensity Difference Over 2 Days (SPID48)
• Sum of Pain Intensity Difference Over 5 Days (SPID120)

9. Statistical Interpretation

10. Statistical Methods Explained

What does the primary mean difference represent?

For each active-treatment group, the reported mean difference compares its posted average SPID72 with the placebo average. A positive difference means the active-treatment group’s observed average score was higher than placebo’s, and higher SPID values indicate greater pain relief. These are unadjusted comparisons: they do not account for baseline characteristics or other covariates in a statistical model. The registry record does not report an adjusted model or a sponsor-reported analysis.

A mean is a summary of the group’s observed scores. The standard deviation describes how spread out individual scores are around that mean; it is not the uncertainty around the mean difference. The posted standard deviations are 132.6 for tapentadol IR, 115.8 for oxycodone IR, and 99.87 for placebo. Considerable variation among individual scores can make a group comparison imprecise, especially when the outcome groups are small.

What does a confidence interval tell the reader?

A confidence interval gives a range of values compatible with the observed data under the method used to calculate it. In general, a wider interval indicates less precision than a narrower interval. For this trial, the primary confidence intervals extend from negative to positive values, so the posted data are compatible with a range that includes effects in either direction. The interval is not a guarantee that the true effect lies within its endpoints, and it does not show the probability that a particular effect is true.

How should a p-value be read?

A p-value describes how unusual data at least as inconsistent with a null hypothesis would be if that hypothesis and the statistical assumptions were correct. It is not the probability that the null hypothesis is true, nor does it measure the size or clinical importance of an effect. The unadjusted p-values for the primary comparisons are 0.43 and 0.597. They do not cross the conventional two-sided 0.05 threshold, but that fact alone cannot establish no effect, equivalence, or similarity between treatments.

Why does the analysis population matter?

The registry defines the modified Intent-to-Treat population using randomization, receipt of at least one dose, and a qualifying baseline pain-intensity assessment. This definition excludes randomized participants who do not meet those conditions. An analysis population should be interpreted according to its stated definition, since changing who contributes data can affect the result. The registry record does not report how many randomized participants were excluded from this population, the extent of missing follow-up measurements, or the method used to address missing data.

Why is the study’s early termination important?

The registry reports slow enrollment and premature termination after 108 of 600 subjects enrolled, and explicitly cautions that valid statistical conclusions cannot be made due to the low number of subjects. Fewer observations generally leave less information for estimating a group difference, which is reflected in the uncertainty of the posted comparisons. Early termination also means the final evidence base is smaller than the planned enrollment, but the registry record does not report interim analyses or a stopping rule. It would be inappropriate to infer either from the fact of termination alone.

What is the role of secondary outcomes?

Secondary outcomes include responder thresholds at specified assessment days and SPID over other time windows. A responder outcome converts a continuous pain measure into a category according to a threshold. Such outcomes can be easier to describe as proportions, but categorization discards information about how far a participant’s score lies above or below the threshold. Testing multiple outcomes can also increase the chance of at least one apparently unusual result. The registry record does not report a multiplicity adjustment or a prespecified hierarchy for secondary testing, so their unadjusted comparisons should be treated as exploratory rather than as separate confirmatory conclusions.

What does “unadjusted” mean in these comparisons?

Unadjusted means that the comparison is calculated from the posted group summaries without accounting for other variables or applying a multiplicity correction. It does not mean the random allocation was ignored in the trial conduct; rather, it describes the calculation used for the displayed comparison. The registry record lists no reported analyses and no details of an original statistical plan, so these calculations cannot be assumed to match the trial team’s intended analysis.

11. Confidence Intervals and Precision

The primary estimates are imprecise. The tapentadol IR versus placebo mean difference is 24.8, with a 95% confidence interval from -36.77 to 86.37. The oxycodone IR versus placebo mean difference is 15.2, with a 95% confidence interval from -41.11 to 71.51. Both intervals cover zero and extend into positive and negative values. Thus, the posted summaries do not pin down either the direction or the size of the difference with much certainty.

In general, a confidence interval describes a range of effect estimates compatible with the data and the calculation method. Greater precision would produce a narrower interval, while limited information and variability can produce a wider one. These intervals are broad relative to the point estimates and allow for materially different interpretations. They should not be read as showing that all values in the interval are equally likely, or as a range that is certain to contain the true effect.

The outcome-group counts were 36.0 for tapentadol IR, 41.0 for oxycodone IR, and 20.0 for placebo. The registry also reports substantial standard deviations for the continuous endpoint. The low enrollment and premature termination noted by the registry are relevant context for the breadth of the intervals. A p-value alone would conceal much of this uncertainty; the effect estimates and intervals are more informative about the range of differences compatible with the posted summaries.

The intervals are unadjusted recalculations from posted summary statistics, rather than confidence intervals from a reported sponsor analysis. The registry record does not provide a sponsor-reported analysis or an analysis plan with which to compare the calculations. The intervals therefore describe the recalculated comparisons, not an independently verified confirmatory analysis.

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 sample-size figures are planning illustrations based on the observed effect, not the trial’s original design. The stated assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is a stated fraction of the observed effect. For these comparisons, the figures are participants per arm; the event-total convention used for time-to-event outcomes does not apply to these continuous and binary outcomes.

The 80% power column describes an illustrative design that would have an 80% probability of detecting the specified effect at the stated significance level if that effect and the assumptions were correct. The 90% power column describes the corresponding target for 90% probability. These are design probabilities under assumptions, not probabilities that the reported treatment effect is true. The planning calculations are not observed power.

Rows that use a smaller fraction of the observed effect require more participants per arm because a smaller difference is harder to distinguish from random variation. The figures depend on treating the observed effect as a reasonable basis for planning, an especially uncertain premise in a prematurely terminated trial with low enrollment and broad confidence intervals. They should be read as illustrations of how assumptions affect planning, not as a reconstruction of the study’s protocol or its intended sample-size justification. The registry record does not report the original design assumptions.

The sample-size values pertain to the comparison and outcome associated with each planning calculation, not to a single universal enrollment target. Equal allocation is an assumption of these illustrations; it should not be taken as evidence that every planned trial feature used that allocation. The registry record’s planned enrollment was 600, but its original statistical rationale for that target is not reported.

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 = 24.800; pooled standard deviation σ = 122.067.
2. n = 2 × (1.96 + 0.842)² × 122.067² / 24.800² = 380.3, rounded up to 381 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 <- 24.8                      # observed difference in means
sigma <- 122.067414024656                     # 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(771758)
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 = 381 (80% power), 510 (90% power)
 75% of observed effect: n per arm = 677 (80% power), 906 (90% power)
 50% of observed effect: n per arm = 1,522 (80% power), 2,037 (90% power)
power.t.test: 381.3 
Simulated power at n = 381 per arm: 0.799 (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. Multiplicity, Missing Data and Analysis Populations

Multiplicity. The registry lists 45 outcome measures and 0 analyses, with 44 secondary outcomes posted. The secondary measures include several responder thresholds at different assessment days and SPID outcomes over different windows. When many outcomes are examined, the chance of obtaining at least one apparently notable result by chance can increase. A prespecified hierarchy or adjustment can address this concern, but the registry record does not report whether either was planned or used. The posted unadjusted secondary results should not be treated as a collection of independent confirmatory tests.

Missing data. The primary analysis population requires a baseline assessment and receipt of at least one dose. The registry record does not report the amount or pattern of missing follow-up data, reasons for missing assessments, or the method used to handle missing values. It also does not report whether participants with incomplete outcome measurements were included in any particular analysis. This limits assessment of how representative the analyzed measurements are of all randomized participants and whether missingness could have affected the estimates.

Analysis populations. The stated modified Intent-to-Treat population consists of randomized patients who took at least one dose and had a baseline pain-intensity assessment through the Interactive Voice Response system with a score of at least 5 on the 11-point scale. That is the registry’s definition for the primary outcome. The record does not report additional analysis populations or detailed participant flow into each outcome analysis. The outcome-group counts therefore describe the posted endpoint results, but the registry record does not provide enough detail to reconcile every randomized participant with each analysis.

The registry’s stated caution that valid statistical conclusions cannot be made due to low enrollment applies to interpretation of the results as a whole. It does not resolve the missing-data or multiplicity questions, for which further methods are not reported in the registry record.

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 serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: cardiac failure congestive (2.3%), cellulitis (2.3%), accidental overdose (2.3%).

The registry reports serious adverse events for groups at risk of 44 in the tapentadol IR group, 43 in the oxycodone IR group, and 21 in the placebo group. The corresponding counts of participants affected by a serious adverse event were 1, 1, and 0. These are event-related safety summaries and should be read separately from the pain endpoint. The group sizes at risk are not the same as the primary outcome counts.

For other adverse events, the counts affected were 23 in the tapentadol IR group, 29 in the oxycodone IR group, and 6 in the placebo group; the numbers at risk were 44, 43, and 21, respectively. The registry lists congestive cardiac failure, cellulitis, and accidental overdose among the top serious-event terms, each reported as 2.3%. The registry record does not report deaths for these groups.

These figures describe what the registry reports, but do not by themselves establish whether an event was caused by a study drug or support a reliable comparison of safety between groups. The study’s early termination and limited enrollment constrain interpretation, and the registry record does not provide enough detail to infer comparative risk from these counts alone.

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

The posted primary results describe average SPID72 scores and unadjusted comparisons of each active-treatment group with placebo. The estimates are positive, but their confidence intervals include zero and extend in both directions. The results therefore leave substantial uncertainty about the size and direction of the group differences. They do not establish that the groups are equivalent, and they do not establish that either active treatment differs from placebo.

This uncertainty is consistent with the registry’s explicit statement that the study was terminated prematurely because of slow enrollment and that valid statistical conclusions cannot be made due to the low number of subjects. The posted data can be described, but they should not be used as a definitive answer to the clinical question. The registry record does not report a sponsor analysis that could provide a different inferential assessment.

The outcome is a time-weighted pain measure over 72 hours. It does not directly establish effects on pain beyond that interval, long-term function, quality of life, or other outcomes not reported in the registry record. Secondary responder results and other SPID windows provide related descriptions, but their unadjusted nature and the number of outcomes make them less conclusive. Safety counts are also descriptive and do not establish causation or comparative safety.

More generally, absence of a statistically significant result is not proof of no effect. Conversely, a numerical difference between group means is not proof that a treatment effect exists. Statistical uncertainty, limitations in the analysis information, and early termination all matter when weighing the posted findings. No treatment recommendation follows from these registry results.

17. Why This Trial Matters Statistically

This trial is statistically informative in part because it makes the difference between a numerical estimate and a conclusive result visible. The posted group means differ, but the uncertainty intervals are broad and include values on either side of no difference. Reporting the estimates alongside intervals helps readers avoid treating a point estimate or p-value as a complete description of the evidence.

The registry also documents a major distinction between intended and achieved enrollment: the study ended early after slow enrollment, with 108 of 600 subjects enrolled. This matters because design plans cannot guarantee that a study will collect enough information to answer its question. The registry explicitly warns that valid statistical conclusions cannot be made because the number of subjects was low, reinforcing the need to interpret the estimates cautiously.

The comparison structure is another useful statistical point. Each active-treatment group is compared with placebo; there is no posted direct comparison between the active treatments. Nor does the registry report a detailed analysis plan, missing-data methods, or multiplicity procedure. These omissions limit what can be inferred from the numerous outcome measures and their unadjusted comparisons.

Finally, the planning illustrations show how required sample sizes depend on the effect size assumed for planning. Those illustrations are not the trial’s original design assumptions and are not observed power. In a trial with uncertain observed effects, planning from the observed estimate should be interpreted particularly cautiously. Together, these features show why statistical interpretation requires attention to design, precision, analysis populations, and reporting—not just the direction of a group mean.

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.

This trial’s central limitation is the premature termination attributed to slow enrollment. The registry reports enrollment of 108 of 600 planned subjects and states that valid statistical conclusions cannot be made because of the low number of subjects. The relatively small outcome groups and broad intervals leave the primary comparisons uncertain.

The registry record lists 45 outcome measures but 0 analyses. Although the primary endpoint and a modified Intent-to-Treat population are described, detailed inferential methods are not reported. The record does not report the trial’s original sample-size assumptions, a full statistical analysis plan, multiplicity handling, or a sponsor-reported analysis. It also does not report how missing follow-up measurements were handled or how many participants contributed to each assessment beyond the posted outcome counts.

The posted primary comparisons are unadjusted recalculations from summary statistics. They do not account for covariates, and the record does not show whether a different prespecified analysis was used by the sponsor. The secondary results involve multiple measures and are also unadjusted, so isolated differences warrant particular caution. The registry does not report a direct active-treatment comparison.

The outcome measures pain over 72 hours for the primary endpoint, with secondary outcomes covering other time windows and responder thresholds. These results do not establish longer-term outcomes. The registry also does not provide enough information to assess the completeness of safety follow-up or to infer causation from adverse-event counts. These limitations restrict the strength and scope of conclusions that can be drawn from this record.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Tapentadol IR vs Oxycodone IR vs Placebo in Acute Pain From Vertebral Compression Fracture Associated With Osteoporosis — NCT00771758.
• Registry record last updated 2014-05-09; status last verified 2014-04.
• Results first posted 2011-04-07.
• 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

The registry describes a randomized, quadruple-masked, parallel-group phase 3 study of tapentadol IR, oxycodone IR, and placebo for acute pain associated with osteoporotic vertebral compression fractures. The primary endpoint was SPID72, a time-weighted summary of pain-intensity differences over 72 hours, with higher values indicating greater pain relief.

The study was completed after premature termination for slow enrollment; 108 of 600 subjects enrolled. The posted primary comparisons are unadjusted recalculations, and their confidence intervals include zero. The registry explicitly cautions that valid statistical conclusions cannot be made because of the low number of subjects. Detailed original design assumptions, missing-data methods, and multiplicity procedures are not reported in the registry record.