Analgesic Effect of Different Combinations of Dexketoprofen Trometamol With Tramadol Hydrochloride in a Model of Moderate to Severe Pain: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Analgesic Effect of Different Combinations of Dexketoprofen Trometamol With Tramadol Hydrochloride in a Model of Moderate to Severe Pain (NCT01307020), a randomized phase 2 study. The primary outcome is Percentage of Patients Achieving at Least 50 % of the Theoretical Maximum Total Pain Relief Score at 6 Hours Post-dosing..

2. Clinical Question

The research question concerns a short-term pain-relief measure after a defined dental procedure. The combination groups varied the doses of both components, allowing the posted results to describe the response in each dose combination as well as in groups receiving one component alone. The active control had a separate role: it was included to check that the study’s pain model could distinguish an active analgesic from placebo. That purpose is stated in the registry summary; it does not establish that any particular comparison met a formal validation criterion.

The principal contrast presented in the recalculated results is each treatment group versus placebo. Those estimates describe observed differences in the proportion meeting the threshold, with confidence intervals and unadjusted p-values. They should be read as comparisons of the posted group results, not as a complete account of the trial’s prespecified analyses. The registry record does not report a full sponsor analysis or a detailed analysis plan.

3. Trial Design

This was a randomized, triple-masked, parallel-group phase 2 study. The registry lists an enrollment of 745 and a completed status. The study evaluated a single oral administration in participants with moderate to severe pain following impacted third mandibular molar extraction. The registered title describes placebo and active controls and comparisons of combination doses with the single agents.

The treatment groups included four combinations of dexketoprofen trometamol and tramadol hydrochloride, two dexketoprofen trometamol single-agent groups, two tramadol hydrochloride single-agent groups, ibuprofen 400mg, and placebo. The posted primary outcome includes group sizes in the range of 59.0 to 63.0. The registry lists no further arm descriptions, so details beyond the treatment names and doses are not reported in the registry record.

Randomization means that treatment assignment is intended to use chance rather than clinical choice. Triple masking indicates that the record describes the study as triple-masked, but it does not identify which participant, investigator, or other roles were masked. Those specifics are not reported in the registry record. A parallel-group design assigns participants to a group whose results are compared with the other groups rather than describing a crossover between treatments.

The stated primary analysis population is the intention-to-treat population, defined as patients who took study treatment and had at least one post-dose assessment. This definition excludes randomized participants without a post-dose assessment, so it is not identical to an analysis of every randomized participant. Further information about missing assessments, exclusions, or handling of incomplete outcome data is not reported in the registry record.

The registry lists secondary measures of pain relief at other post-dose times and use of rescue medication. The numerical secondary results posted include rescue medication use through 6 hours. Numerical results for the listed pain-relief measurements at other times are not reported in the registry record. The registry does not report the original sample-size justification or detailed statistical analysis plan.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Before assignment: The trial encompassed 3 visits: 1-Screening; 2-Dental surgery (patients who have moderate to severe pain afterwards were randomised and received study drug); 3-End of study. Overall, 745 patients were enrolled (screened), of them 611 were randomized to receive the study drug and therefore considered as started.

Only the first 6 of 10 groups are shown.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: ITT (intention to treat) population which was defined as all patients who have taken the study treatment and have at least 1 post-dose assessment

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.

Only the first 6 of 11 groups are shown.

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Patients Achieving at Least 50 % of the Theoretical Maximum Total Pain Relief Score at 6 Hours Post-dosing., measured over 6 hours.

The primary endpoint is the percentage of patients who achieved at least 50 % of the theoretical maximum total pain relief score at 6 hours post-dosing. Pain relief was measured on a verbal rating scale from 0=none to 4=complete. The theoretical maximum total pain relief score over 6 hours is defined in the record as 24, calculated by summing the maximum analgesia scores at the specified assessment times. The endpoint turns those repeated pain ratings into a binary outcome: each patient either reached the stated threshold or did not.

A threshold-based endpoint can make a result easier to interpret as the share of participants reaching a defined level of relief, rather than as an average score across participants. It also discards information about how far an individual’s score was above or below the threshold. Two groups could have similar percentages reaching the threshold while differing in the underlying scores, or vice versa. The registry does not provide the individual scores or a distribution of total pain relief values, so those details cannot be assessed.

The endpoint is measured at a specific follow-up time and is reported for the intention-to-treat population defined by the registry. It is a measure of observed pain relief in this procedural pain model, not a general measure of pain in other settings. Nor does the endpoint alone capture other outcomes such as rescue medication use, adverse events, or pain relief at later times. The registry lists additional pain-relief assessments at other times, but their numerical results are not reported in the registry record.

7. Results Posted in the Registry

• DKP-TRIS 12.5mg - TRAM.HCl 37.5mg: 36.7% (22/60) versus 9.7% (6/62) on control; risk difference 27.0 percentage points (95% CI 12.7 to 41.2), risk ratio 3.79 (1.65–8.69); unadjusted two-proportion z-test p = <0.001.
• DKP-TRIS 12.5mg - TRAM.HCl 75mg: 59.7% (37/62) versus 9.7% (6/62) on control; risk difference 50.0 percentage points (95% CI 35.7 to 64.3), risk ratio 6.17 (2.81–13.55); unadjusted two-proportion z-test p = <0.001.
• DKP-TRIS 25mg - TRAM.HCl 37.5mg: 55.6% (35/63) versus 9.7% (6/62) on control; risk difference 45.9 percentage points (95% CI 31.6 to 60.2), risk ratio 5.74 (2.60–12.67); unadjusted two-proportion z-test p = <0.001.
• DKP-TRIS 25mg - TRAM.HCl 75mg: 72.1% (44/61) versus 9.7% (6/62) on control; risk difference 62.5 percentage points (95% CI 49.0 to 75.9), risk ratio 7.45 (3.43–16.20); unadjusted two-proportion z-test p = <0.001.

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.

Percentage of Patients Using Rescue Medication at 6 Hours

• 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:
  • DKP-TRIS 12.5mg - TRAM.HCl 37.5mg: 66.7% (40/60) versus 72.6% (45/62) on control; risk difference -5.9 percentage points (95% CI -22.2 to 10.4), risk ratio 0.92 (0.73–1.16); unadjusted two-proportion z-test p = 0.477.
  • DKP-TRIS 12.5mg - TRAM.HCl 75mg: 46.8% (29/62) versus 72.6% (45/62) on control; risk difference -25.8 percentage points (95% CI -42.5 to -9.1), risk ratio 0.64 (0.47–0.88); unadjusted two-proportion z-test p = 0.003.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between DKP-TRIS 12.5mg - TRAM.HCl 37.5mg and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for DKP-TRIS 12.5mg - TRAM.HCl 75mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes broaden the description beyond the primary threshold at 6 hours. The registry lists the percentage achieving a specified pain-relief threshold at other post-dose times and the percentage using rescue medication by 6 hours. Numerical results posted for rescue medication show a general pattern in which the combination groups have lower observed use than placebo. The single-agent groups and ibuprofen also provide context, but the values vary across these groups. The listed pain-relief measurements at the other times are not reported in the registry record.

Lower rescue medication use is directionally consistent with a pattern of greater observed pain relief in the combination groups on the primary measure, but the outcomes are not interchangeable. Reaching a pain-score threshold and using rescue medication are different events, and rescue medication use may reflect factors beyond the score itself. The registry does not provide enough detail to establish how rescue medication was handled in the primary endpoint analysis or whether use was interpreted as treatment failure.

The recalculated inferential comparisons posted for rescue use cover only a subset of the treatment contrasts. One is not statistically distinguishable from no difference by its unadjusted comparison, while the other has an unadjusted p-value below 0.05. These secondary comparisons should carry less weight than a prespecified primary analysis because they add hypotheses, are not adjusted for multiplicity in the posted calculations, and may not represent the sponsor’s analysis. Their results are best viewed as supporting context rather than independent confirmation of the primary finding.

Assessments at different times and multiple types of outcome can add useful information, but they also increase the number of opportunities to find a nominally small p-value. The registry does not report how these secondary hypotheses were prioritized, whether any were confirmatory, or whether multiplicity was addressed. That uncertainty limits how strongly secondary patterns can be interpreted.

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

• Percentage of Patients Achieving at Least 50 % of the Theoretical Maximum Total Pain Relief Score at 4, 8 and 12 Hours Post-dosing.
• Percentage of Patients Using Rescue Medication at 6 Hours

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary: a participant either achieved at least 50 % of the theoretical maximum total pain relief score by 6 hours or did not. The registry reports the percentage in each treatment group, and the recalculated comparisons express the difference between each group and placebo as a risk difference. A risk difference describes the absolute separation between two event proportions on the proportion scale. It is distinct from a relative measure, such as a risk ratio, which compares proportions as a ratio. The principal interpretation uses the risk difference because it describes the between-group gap directly.

What does the confidence interval describe?

A confidence interval gives a range of values compatible with the data under the statistical procedure used. It communicates the uncertainty in an estimated comparison: narrower intervals indicate greater precision, while wider intervals indicate greater uncertainty. For a risk difference, an interval that includes no difference is compatible with no group separation as well as with effects in either direction. An interval that does not include no difference indicates that the data are less compatible with no difference under the calculation used. This general explanation does not resolve the separate question of adjustment for multiple comparisons.

The registry posts a control group and arm-level percentages, but the sponsor’s analysis results and methods are not reported. The displayed pairwise estimates are recalculated, unadjusted comparisons from the posted summary statistics. The registry record does not describe whether the original analysis used covariate adjustment, a particular hypothesis-testing procedure, or other model specifications. As a result, these calculations offer a transparent comparison of the reported summaries but cannot substitute for a complete prespecified analysis.

How should the p-values be read?

A p-value measures how unusual data at least as incompatible with a specified null hypothesis would be under that hypothesis and the calculation’s assumptions. It is not the probability that the null hypothesis is true, and it does not quantify the size or importance of a difference. The p-values in the recalculated comparisons are unadjusted. Several treatment groups are compared with placebo, and the record does not say whether or how the original analysis controlled the chance of false-positive findings across the family of comparisons. Thus, a small unadjusted p-value should be read as evidence from that single comparison, not as a multiplicity-adjusted conclusion for the whole set.

The endpoint’s binary form is relevant to the statistical method: the event is reaching the specified threshold, and the group percentage is the proportion with that event. A risk difference is one way to summarize the contrast. Other summaries, including risk ratios and odds ratios, are also listed in the recalculated results. They answer different questions and can have different numerical scales. The registry does not report which comparison measure was the sponsor’s primary analysis measure, so the recalculated risk difference should not be represented as the sponsor’s chosen estimand.

What population is represented?

The primary outcome population is defined as all patients who took study treatment and had at least one post-dose assessment. This is the registry’s stated intention-to-treat definition. In general, an intention-to-treat approach aims to preserve the randomized comparison, but this particular definition requires a post-dose assessment and therefore does not include every randomized participant by definition. The record does not describe how missing outcomes were handled, how many patients lacked an assessment, or whether any other analysis populations were used. Those details matter because exclusions or missing outcomes can affect how closely the analyzed groups retain the balance created by randomization.

The trial is described as randomized, triple-masked, and parallel-group. Random assignment helps reduce systematic differences between groups at the outset, while masking can limit influences on reporting or assessment. The record does not state which roles were masked or give details of the randomization procedure, so further methodological claims cannot be made from the available description.

What does a planning calculation mean?

The sample-size illustrations are based on the observed effect in a comparison and show hypothetical participants per arm for stated power targets and fractions of that effect. The assumptions listed for those illustrations are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. These are planning calculations, not a report of the original design process. The trial’s own sample-size assumptions and justification are not reported in the registry record. Smaller effects require more participants to detect under these planning assumptions. These projected sample sizes are not observed power and do not establish the probability that the actual trial detected a true effect.

Finally, the randomized study includes several arms and more than one outcome, but the registry does not report a complete statistical plan, interim-analysis details, or a missing-data strategy. These absences constrain how much can be inferred about prespecification and robustness. The numerical comparisons remain useful descriptions of the posted endpoint, provided their recalculated and unadjusted status is kept clear.

11. Confidence Intervals and Precision

Precision concerns how much uncertainty remains around an estimated difference. For the primary comparisons against placebo, confidence intervals are reported for the recalculated risk differences. The intervals for the combination groups are on the positive side of no difference; their widths still show that the size of each estimated separation is uncertain. Confidence intervals for the single-agent comparisons are more varied: some do not include no difference, while the interval for tramadol hydrochloride 37.5mg spans it. These statements describe the recalculated intervals and do not account for any multiplicity adjustment.

The arm percentages are based on group sizes around 60 participants. With group sizes of this scale, a small change in the number of people reaching the threshold can noticeably change a percentage. The confidence intervals are therefore important alongside the point estimates. The largest observed percentage is not necessarily the most precisely estimated result, and a difference between point estimates is not itself evidence that the treatments differ statistically.

The endpoint is binary and measured at one primary time point. Its confidence interval concerns the group comparison for the proportion crossing the threshold, not the full distribution of pain-relief scores or the precision of other outcomes. No confidence intervals are posted for the arm-level percentages themselves in the registry results. The recalculated intervals also rely on summary data and should not be mistaken for the sponsor’s analysis intervals.

Precision is distinct from clinical importance. An interval can help assess plausible statistical values for the comparison, but the registry does not state a threshold for a clinically important difference. The intervals also do not address uncertainty from outcome selection, missing data, multiplicity, or generalizability beyond the study’s setting.

12. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The planning figures for these binary outcomes are participants per arm, not total participants across both comparison groups and not total events. They illustrate how many participants might be needed under stated assumptions to detect a chosen fraction of the observed effect. The assumptions listed are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. For the time-to-event case, the stated convention would instead be total events, but the outcomes discussed in this study are not time-to-event outcomes.

The 80% power column gives a planning count associated with an 80% chance of detecting the specified effect if that effect were the true one and the assumptions held. The 90% power column uses a higher target chance of detection and therefore generally calls for more participants. The calculations use the observed effect as their starting point, then consider planning for 100% of that observed effect, 75% of the observed effect, or 50% of the observed effect. Planning for a smaller effect requires more participants, because a smaller separation between groups is harder to distinguish from random variation.

Some projections are very large when the observed difference is close to zero. This reflects how difficult it would be to detect a small effect using the stated approach; it is not a claim that such a study was conducted or that the original trial was designed with those group sizes. The original trial’s sample-size justification and design assumptions are not reported in the registry record. These figures are planning illustrations based on observed results, not observed power.

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, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.097; treatment proportion p₁ = 0.367; average p̄ = 0.232.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5967 = 1.1695.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5654 = 0.4758.
4. n = (1.1695 + 0.4758)² / (0.2699)² = 37.2, rounded up to 38 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 <- 0.0967741935483871                          # control proportion
p1 <- 0.366666666666667                          # 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(1307020)
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 = 38 (80% power), 50 (90% power)
 75% of observed effect: n per arm = 60 (80% power), 80 (90% power)
 50% of observed effect: n per arm = 118 (80% power), 157 (90% power)
power.prop.test: 37.2 
Simulated power at n = 38 per arm: 0.827 (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.

14. Multiplicity, Missing Data and Analysis Populations

The trial compares several treatment groups with placebo and includes secondary outcomes. Each additional comparison creates another opportunity for a nominally small p-value to occur by chance, even if there is no true group difference. Statistical methods can address this issue by defining a family of hypotheses and adjusting the interpretation or testing procedure. The registry record does not report whether the sponsor adjusted for multiplicity, which comparisons were considered primary beyond the stated primary endpoint, or how secondary hypotheses were ordered.

The recalculated p-values are explicitly unadjusted. They describe individual comparisons and should not be interpreted as controlling the overall false-positive risk across the treatment groups and outcomes. The registry reports no sponsor analyses in the posted analysis list. Details of the sponsor’s statistical analysis plan, including any testing hierarchy, interim analyses, or multiplicity procedure, are not reported in the registry record.

Missing-data handling is also not reported. The primary population definition requires a post-dose assessment, but the registry does not state how many participants were randomized but lacked one, whether any endpoint assessments were missing after treatment, or how incomplete outcomes were treated. It does not describe imputation, sensitivity analyses, or other methods for evaluating the effect of missingness. Without those details, the potential influence of missing outcome data cannot be judged.

The listed population is an intention-to-treat population defined by treatment exposure and at least one post-dose assessment. This differs from a strict all-randomized population if randomized participants did not take treatment or had no post-dose assessment. The registry does not report other analysis populations, such as per-protocol or safety populations, beyond the group-specific adverse-event counts. Nor does it give a detailed flow of participants through the study.

These are reporting limitations, not evidence that any particular method was or was not used. They mean that the recalculated comparisons can be read as descriptive, unadjusted evidence from the posted summaries, while claims about prespecification, multiplicity control, missing-data robustness, or concordance with the sponsor’s analysis cannot be verified from 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: dizziness (1.7%).

The serious adverse-event counts are reported by treatment group. The record lists zero serious adverse events in every group except TRAM.HCl 75mg, where one participant was affected among 60 at risk. No serious adverse events are listed for the combination groups, dexketoprofen trometamol groups, ibuprofen, or placebo. A zero in these observed counts does not establish that the risk is absent; it indicates only that none were recorded for those groups in the posted results.

The record lists dizziness at 1.7% among the top serious adverse-event terms. It does not provide further detail about the event’s timing, severity, or relationship to treatment. Death counts are not reported in the registry record. The group sizes are modest, and serious events are uncommon in the posted counts, so these data have limited precision for comparing safety between groups.

Other adverse events are tabulated separately from serious adverse events. The registry lists affected-participant counts for these other events, but the serious-event figures should not be conflated with them. These counts are descriptive and do not by themselves establish comparative safety, causation, or a complete assessment of harms.

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

The registry results show that the percentage reaching the primary pain-relief threshold differed across the treatment groups at 6 hours. The combination groups had higher observed percentages than placebo, and their recalculated unadjusted comparisons had p-values <0.001. The active control and single-agent groups provide additional context, with results that vary by dose and component. The posted data therefore describe differences in this specific endpoint and study setting.

Those observations do not establish that any treatment works or does not work in general. The endpoint is a threshold based on a verbal pain-relief scale, measured over a short interval after a specific dental procedure. It is not a full account of pain scores, other symptoms, later outcomes, or individual experience. The registry does not provide numerical results for the listed pain-relief assessments at other times.

The results also do not establish that one active treatment is superior to another. The reported recalculations compare each group with placebo; they do not provide all pairwise active-treatment contrasts. Nor do the posted p-values address multiplicity. The lack of a detailed sponsor analysis, missing-data information, and a stated multiplicity approach limits the strength of any broad inferential conclusion.

The inclusion of ibuprofen as an active control was intended to validate the pain model, according to the registry summary. The record does not report a formal validation test or criterion, so the observed ibuprofen result alone cannot be taken as proof that the model was validated.

Finally, the registry reports a limited set of serious adverse-event counts and other adverse-event counts. These findings do not establish comparative safety, particularly given the group sizes and the absence of further detail. Interpretation should remain bounded by the one-dose, post-extraction study, the defined 6-hour primary outcome, and the information actually reported in the registry record.

17. Why This Trial Matters Statistically

This trial is statistically notable for its multi-arm comparison of dose combinations alongside the individual components, placebo, and an active control. That design makes the pattern across groups informative, but it also creates multiple comparisons. The distinction between a broad descriptive pattern and adjusted confirmatory evidence is important: the recalculated comparisons are unadjusted, and the registry does not describe a multiplicity plan.

The primary endpoint is a binary threshold derived from a pain-relief score. This illustrates a common trade-off in clinical outcome design. A threshold can make the result understandable as the share of participants reaching a defined level, while losing detail about the underlying score values. Readers should therefore distinguish the proportion crossing the threshold from the full distribution of pain relief.

The record also demonstrates why estimates and their precision matter alongside p-values. A p-value addresses compatibility with a null hypothesis under a calculation; it does not state the size of a difference or its precision. Confidence intervals give information about uncertainty in the recalculated risk differences, while the modest group sizes and absent arm-level intervals limit some aspects of interpretation.

Finally, planning projections based on observed effects are not a substitute for the original design rationale. They illustrate how sample-size needs change with the effect assumed for planning, but the registry does not report the original justification. Separating these post-result planning illustrations from actual prospective design decisions is essential for avoiding an overstatement of what the study was designed to detect.

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.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

The most important trial-specific limitation is the restricted setting: the study assessed a single oral administration following impacted third mandibular molar extraction, with a primary assessment at 6 hours. The findings do not directly describe repeated dosing, other causes of pain, or outcomes beyond the reported observation period. The registry summary does not provide further details about the procedure, clinical setting, or participant characteristics.

The primary measure reduces a pain-relief score to whether a participant reached a threshold. This makes the proportion easy to describe but does not show the distribution of scores or the amount of relief among those who did and did not meet the threshold. The numerical results for other registered pain-relief timepoints are not reported in the registry record, limiting assessment of how the pattern changes over time.

There are multiple treatment groups, and the registry does not report a multiplicity plan. The available pairwise results are unadjusted recalculations rather than a reported sponsor analysis. The original sample-size justification, detailed statistical plan, missing-data methods, and participant flow are also not reported in the registry record. These gaps prevent a full assessment of prespecification, robustness, and the effect of incomplete outcomes.

The reported group sizes are modest, and the serious adverse-event counts are sparse. Consequently, the safety counts provide limited information for comparative inference. The record also does not provide detailed event-level descriptions or report deaths. Finally, while ibuprofen was included to validate the pain model, the registry does not give a formal validation analysis. Each of these limitations narrows what can responsibly be concluded from the posted results.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Analgesic Effect of Different Combinations of Dexketoprofen Trometamol With Tramadol Hydrochloride in a Model of Moderate to Severe Pain — NCT01307020.
• Registry record last updated 2013-08-12; status last verified 2013-07.
• Results first posted 2012-12-10.
• 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

NCT01307020 is a completed, randomized, triple-masked, parallel-group phase 2 study with enrollment of 745. It evaluated single oral administrations of dexketoprofen trometamol and tramadol hydrochloride in combination and as single agents, with ibuprofen and placebo controls, for moderate to severe pain after impacted third mandibular molar extraction.

The primary outcome was the percentage achieving at least 50 % of the theoretical maximum total pain relief score at 6 hours. The posted arm percentages range from 9.7% for placebo to 72.1% for the DKP-TRIS 25mg - TRAM.HCl 75mg group. Recalculated comparisons with placebo are unadjusted. The registry also lists rescue medication use and other pain-relief timepoints, but numerical results for the other pain-relief times are not reported in the registry record.

The registry record does not report the sponsor’s detailed analysis plan, multiplicity handling, missing-data methods, or original sample-size justification. Serious adverse-event counts are sparse, with one affected participant in the TRAM.HCl 75mg group and zero reported in the remaining groups.