RCT Comparing the Analgesic Efficacy of 4 Therapeutic Strategies Based on 4 Different Major Opioids (Fentanyl, Oxycodone, Buprenorphine vs Morphine) in Cancer Patients With Moderate/Severe Pain, at the Moment of Starting 3rd Step of WHO Analgesic Ladder.: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for RCT Comparing the Analgesic Efficacy of 4 Therapeutic Strategies Based on 4 Different Major Opioids (Fentanyl, Oxycodone, Buprenorphine vs Morphine) in Cancer Patients With Moderate/Severe Pain, at the Moment of Starting 3rd Step of WHO Analgesic Ladder. (NCT01809106), a randomized phase 4 study. The primary outcome is Proportion of Non-Responder (NR) Participants.

2. Clinical Question

The study asks whether the proportion of participants classified as non-responders after starting a major opioid strategy differs between morphine and three other opioid strategies: oxycodone, buprenorphine, and fentanyl. The clinical context is cancer pain in participants at the point of starting the third step of the WHO analgesic ladder. The primary outcome was assessed over 28 days.

The registry defines non-response as absence of an analgesic effect using pain-intensity-difference information and includes cases in which average pain intensity was stable or worsened at day 28 compared with baseline. The comparison is therefore about the recorded responder classification over the stated follow-up, not every aspect of pain control, tolerability, or longer-term treatment experience.

The study description also identifies dose changes, switching, and permanent treatment abandonment as topics of interest. Results for those topics are not reported in the registry record in the available outcome details. The primary question that can be assessed statistically is consequently the comparative pattern in the posted non-responder counts and risk-difference estimates.

3. Trial Design

The registry describes a Phase 4 randomized, parallel-group trial with no masking. It reports total enrollment of 518 participants and lists four treatment strategies: morphine, oxycodone, buprenorphine, and fentanyl. The sponsor is the Mario Negri Institute for Pharmacological Research. The record gives a start date of 2011-04, a primary completion date of 2014-10, and a completed status.

Random allocation means the treatment strategy was assigned by chance rather than chosen solely by the participant or clinician. In general, randomization can reduce systematic differences between groups at the point of assignment, although it does not ensure that every relevant characteristic is balanced in a particular trial. The parallel model means participants were assigned to a strategy rather than all participants following each strategy in sequence. The record does not report the randomization method or details about allocation concealment.

The study was unmasked: participants and study personnel were not described as blinded to the assigned strategy. Lack of masking can matter for outcomes influenced by expectations, decisions about care, or judgments made during follow-up. The primary outcome is based on pain-intensity reports, so awareness of treatment assignment is relevant context when interpreting the result. The record does not report procedures intended to limit such influence.

Reported group sizes for the primary endpoint were 122 for morphine, 125 for oxycodone, 127 for buprenorphine, and 124 for fentanyl. These are endpoint group counts, not a substitute for details about participant flow. Reasons for any difference between enrollment and the endpoint group counts are not reported in the registry record. Original design assumptions, including the trial’s own sample-size justification, are also not reported in the registry record.

The record identifies an intention-to-treat population for the primary outcome, but it does not describe how missing endpoint measurements were handled or whether every randomized participant was included in the posted counts. The trial’s protocol-level statistical methods, including any planned adjustment for multiple comparisons, are not reported in the registry record.

4. Participant Flow and Accounting

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

Overall Study

Analysis population for the primary outcome, as defined in the registry: Intention-to-treat

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 Proportion of Non-Responder (NR) Participants, measured over 28 days.

The primary endpoint is the number of participants classified as non-responders at 28 days. The registry describes non-responders as participants who report no analgesic effect, based on pain-intensity-difference information measured using a 0–10 NRS. The stated definition includes average pain intensity that is stable or worse at day 28 than at baseline. The registry’s wording for the P.I.D. threshold is recorded as =/< 0%, so the exact notation is retained rather than reinterpreted.

This endpoint converts pain reports into a binary classification: a participant is counted as a non-responder or is not. A binary endpoint is useful for communicating the frequency of a defined outcome in each group and for comparing those frequencies. It does not preserve the full range of pain scores or show how much an individual participant’s pain changed. Participants grouped on the same side of the classification can have different experiences that the count does not distinguish.

The intention-to-treat label indicates the population named for the primary assessment, but the registry does not give enough detail to determine how missing observations or deviations from assigned treatment were handled. The endpoint is limited to the specified 28-day assessment; it does not by itself describe longer-term outcomes, dose changes, switching, or treatment discontinuation.

7. Results Posted in the Registry

• Oxycodone: 14.4% (18/125) versus 11.5% (14/122) on control; risk difference 2.9 percentage points (95% CI -5.4 to 11.3), risk ratio 1.25 (0.65–2.41); unadjusted two-proportion z-test p = 0.494.
• Buprenorphine: 11.0% (14/127) versus 11.5% (14/122) on control; risk difference -0.5 percentage points (95% CI -8.3 to 7.4), risk ratio 0.96 (0.48–1.93); unadjusted two-proportion z-test p = 0.910.
• Fentanyl: 8.9% (11/124) versus 11.5% (14/122) on control; risk difference -2.6 percentage points (95% CI -10.2 to 4.9), risk ratio 0.77 (0.37–1.64); unadjusted two-proportion z-test p = 0.499.

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.

Proportion of Full-responder

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Oxycodone: 72.0% (90/125) versus 73.0% (89/122) on control; risk difference -1.0 percentage points (95% CI -12.1 to 10.2), risk ratio 0.99 (0.85–1.15); unadjusted two-proportion z-test p = 0.867.
  • Buprenorphine: 74.8% (95/127) versus 73.0% (89/122) on control; risk difference 1.9 percentage points (95% CI -9.1 to 12.8), risk ratio 1.03 (0.88–1.19); unadjusted two-proportion z-test p = 0.739.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Oxycodone 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 Buprenorphine and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary endpoint is the proportion of full responders at 28 days. The overall counts across the four arms are in a relatively similar range, and the available pairwise risk-difference estimates for oxycodone and buprenorphine have confidence intervals that include zero. The record does not list a full-responder comparison for fentanyl. These are descriptive patterns rather than a separate, conclusive account of comparative effectiveness.

The secondary endpoint complements the primary non-responder outcome because it focuses on full response rather than absence of an analgesic effect. It does not reproduce the primary endpoint: the record does not explain how participants who are neither full responders nor non-responders are categorized, nor does it report a joint analysis of the response classifications. The secondary findings therefore should be read alongside, but not substituted for, the primary result.

Unadjusted secondary results carry less weight for confirmatory interpretation because they may be among several comparisons examined, increasing the opportunity for chance findings. The registry does not report a multiplicity strategy or an inferential hierarchy for the outcomes. It also lists no reported analyses for the secondary outcome. Without those details, the posted secondary comparisons are best treated as exploratory evidence that can inform a broader reading of the record, rather than as independent proof of a treatment difference.

The secondary endpoint does not resolve the uncertainty in the primary endpoint. Both sets of available comparisons show substantial statistical uncertainty, and the registry record does not report additional secondary outcome analyses that would clarify durability, dose changes, switching, or treatment abandonment.

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

• Proportion of Full-responder

9. Statistical Interpretation

10. Statistical Methods Explained

The posted comparisons use risk differences for binary outcomes. A risk difference expresses the difference between the proportion with the event in one group and the proportion with the event in the comparator group. For the primary endpoint, the event is classification as a non-responder. The direction depends on the ordering of groups: positive estimates indicate a higher event proportion in the named treatment group than in morphine, while negative estimates indicate a lower event proportion.

What does randomization contribute?

Random assignment is intended to make treatment groups comparable on average with respect to both measured and unmeasured characteristics at baseline. It supports a causal interpretation when allocation is implemented as planned and follow-up and analysis preserve the benefits of assignment. It cannot guarantee perfect balance, and it does not correct problems caused by missing outcomes, changes after assignment, or biased measurement. The registry identifies the study as randomized but does not describe the allocation sequence, concealment, or the handling of deviations in enough detail to assess those procedures.

Why use a risk difference?

The risk difference is expressed on the absolute probability scale, so it describes how far apart the observed event proportions are. It can be more directly interpretable than a relative measure when considering the size of an observed difference. Its value depends on the event frequency in both groups, and its uncertainty should be considered alongside the point estimate. The record also lists relative risk and odds-ratio estimates, but the primary posted comparison emphasized is the risk difference. No adjusted model estimates are listed.

What does a confidence interval convey?

A confidence interval gives a range of estimates compatible with the data under the method used to construct it. It reflects sampling uncertainty, not every source of uncertainty: it does not account automatically for limitations such as unmasked assessment, missing outcomes, outcome-definition choices, or selective reporting. A wide interval indicates that the estimate is not precise enough to distinguish among a broad range of possible differences. An interval that includes zero does not establish that the true difference is exactly zero; it indicates that zero is among the values compatible with the interval.

How should the p-values be read?

The registry lists unadjusted p-values for the primary pairwise comparisons. A p-value measures how unusual data at least as extreme as those observed would be under a specified null model; it is not the probability that the null hypothesis is true, and it does not measure the clinical importance of a difference. The values should be interpreted together with the estimates, intervals, group counts, and study limitations. Because the values are unadjusted, they do not account for the possibility of chance findings arising across multiple comparisons.

Why can over-dispersion matter?

Over-dispersion is a general concern for count or proportion data when observed variability is greater than a model assumes. If a method underestimates variability, its intervals may be too narrow and its tests may be too optimistic. The posted primary endpoint is binary, and the record does not report a model or an over-dispersion assessment. There is therefore no basis in the registry record to say that over-dispersion was evaluated or that a particular correction was used. This general concept is relevant when assessing statistical methods, but it should not be mistaken for a reported feature of this trial.

What can be said about analysis populations?

The primary endpoint names an intention-to-treat population. In general, an intention-to-treat analysis aims to retain participants in the groups to which they were assigned, regardless of subsequent treatment changes, preserving the comparison created by randomization. The registry does not report the operational details needed to establish how this principle was implemented, including how missing outcome measurements were treated. It also does not report a separate per-protocol analysis or sensitivity analyses for missing data.

The registry lists no reported analyses for the secondary outcome. It includes posted counts and comparison estimates for some secondary contrasts, but no additional analysis details. The specific confidence-interval construction, test procedure, handling of multiple comparisons, and any covariate adjustment are not reported in the registry record. These omissions mean the posted estimates can be described, but the analytic procedures cannot be reconstructed from the record.

11. Confidence Intervals and Precision

Precision is reflected in the width of the confidence interval around each estimated risk difference. The primary comparison intervals are -0.054 to 0.113 for oxycodone versus morphine, -0.083 to 0.074 for buprenorphine versus morphine, and -0.102 to 0.050 for fentanyl versus morphine. Each interval includes zero, so the posted data are compatible with no difference and with nonzero differences in either direction.

The intervals also span values that would represent different magnitudes of comparative effect. This means the point estimates should not be treated as exact readings of the underlying difference. In particular, an estimate near zero does not on its own demonstrate equivalence or rule out meaningful differences. Equivalence or non-inferiority would require an appropriate design, a prespecified margin, and a corresponding analysis; such information is not reported in the registry record.

The primary endpoint counts are relatively small in each arm, and the number of recorded non-responder events is limited. For binary outcomes, fewer events generally leave more sampling uncertainty around an estimate. The confidence intervals make that uncertainty visible. They should be read as ranges of statistical compatibility under the analysis method, not as guarantees that the true value lies within them or as descriptions of individual participant outcomes.

The registry does not report the interval-construction method, and it does not provide adjusted estimates. The posted intervals therefore should be interpreted in the context of the unadjusted comparisons and the limitations of the record. They quantify statistical uncertainty under the stated comparison, but they do not address possible bias from lack of masking, missing data, outcome measurement, or unreported analysis choices.

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 are illustrations based on the observed effect, not the trial’s original design assumptions. They use a two-sided significance level of 0.05, equal allocation between the two groups, and a normal approximation. The effect to detect is set as the stated fraction of the observed effect. For these non-time-to-event outcomes, the reported sample-size figures are participants per arm, not a combined total. The time-to-event convention does not apply to these binary endpoints.

The 80% power column gives the number of participants per arm that the planning calculation would require to have an 80% chance of detecting the assumed difference under its specified conditions, if that difference were the true effect. The 90% column uses a higher target probability of detection and therefore generally calls for a larger planned group size. These are design quantities under assumptions, not descriptions of what happened in the completed trial.

Rows that use a smaller fraction of the observed effect represent planning for a more modest difference. Smaller effects are harder to distinguish from random variation, so they require more participants to reach the same target power under otherwise unchanged assumptions. This relationship is visible across the planning scenarios and is especially important when the observed difference is small.

These calculations are not observed power. They do not show the probability that the completed trial detected an effect, and they do not validate the observed result. They are planning illustrations tied to the observed effect and the listed assumptions. The trial’s own original sample-size assumptions and justification are not reported in the registry record.

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 = 0.115; treatment proportion p₁ = 0.144; average p̄ = 0.129.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.4746 = 0.9303.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4742 = 0.3991.
4. n = (0.9303 + 0.3991)² / (0.0292)² = 2,066.1, rounded up to 2,067 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 <- 0.114754098360656                          # control proportion
p1 <- 0.144                          # 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(1809106)
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 = 2,067 (80% power), 2,766 (90% power)
 75% of observed effect: n per arm = 3,586 (80% power), 4,799 (90% power)
 50% of observed effect: n per arm = 7,867 (80% power), 10,530 (90% power)
power.prop.test: 2066.1 
Simulated power at n = 2,067 per arm: 0.806 (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 study has four randomized strategies, with morphine serving as the comparator for the posted primary contrasts. Multiple pairwise comparisons and more than one outcome create a multiplicity issue: the more statistical questions examined, the greater the chance that at least one apparently notable result arises by chance, even when no true effect exists. The record does not report whether the trial prespecified a testing hierarchy, adjusted significance levels, or used another method to control multiplicity. The posted p-values are unadjusted.

The registry identifies non-responder proportion as the primary outcome and full-responder proportion as a secondary outcome. It also lists three outcome measures in total, while the available result detail names the primary endpoint and the full-responder endpoint. The status and definition of any additional outcome measure are not reported in the registry record. No reported analyses are listed for the secondary outcome, despite the posted counts and some comparison estimates. The protocol’s planned analysis population, endpoint hierarchy, and analysis plan are not reported in the registry record.

The primary outcome population is labeled intention-to-treat. The record does not explain whether every randomized participant contributed an endpoint value, how missing pain assessments were handled, or whether any imputation or sensitivity analysis was used. The endpoint group counts are reported, but participant flow and reasons for any unavailable measurements are not described. Missing outcomes can affect a randomized comparison if their occurrence is related to treatment assignment or outcome status, and the direction of any such influence cannot be determined from the posted record.

The record also does not report interim analyses, stopping rules, adjusted analyses, or a protocol-level sample-size justification. These matters should not be inferred from the completed status or from the planning illustrations. Their absence limits assessment of the prespecified analysis process and the extent to which the reported comparisons reflect all planned analyses.

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: hyperpyrexia (1.6%), bowel occlusion (0.8%), dyspnea (0.8%), hyperalgesia (0.8%), atelectasis (0.8%).

The registry reports serious adverse events for each treatment group: 5 of 122 participants in the morphine group, 1 of 125 in the oxycodone group, 1 of 127 in the buprenorphine group, and 5 of 124 in the fentanyl group. The counts of participants with other adverse events are 103 of 122, 98 of 125, 108 of 127, and 95 of 124, respectively. These are group-level counts, not estimates adjusted for differences in follow-up or exposure.

The registry lists serious adverse-event terms including hyperpyrexia at 1.6%, and bowel occlusion, dyspnea, hyperalgesia, atelectasis, and exitus at 0.8% each. These term frequencies should not be assumed to represent all event types or to establish that an event was caused by a particular treatment. The record does not report deaths by group; the death counts are not reported in the registry record.

Adverse-event counts are descriptive safety data. The registry does not give comparative statistical tests or adjusted safety estimates in the available record. Differences in the counts should therefore not be interpreted as proof of a safety advantage or disadvantage. The figures also do not replace details about event severity, timing, exposure, or how events were collected, which are not reported in the registry record.

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

The results describe the observed 28-day non-responder counts and unadjusted comparisons among participants assigned to four opioid strategies. The primary risk-difference point estimates vary in direction, and all three confidence intervals include zero. The data therefore do not sharply distinguish the non-responder proportions between morphine and each of the other strategies. At the same time, the intervals are broad enough to remain compatible with differences in either direction, so absence of a clear statistical separation is not evidence that the strategies are equivalent.

The result is specific to the registry’s non-responder definition, the recorded follow-up, and the analyzed participants. It does not establish how participants’ pain changed across the full scale, the extent of dose adjustment, or how often participants switched or permanently stopped treatment. Those topics appear in the study description, but the corresponding outcomes are not reported in the registry record in the available results.

Interpretation is also constrained by the open-label design. Participants and study personnel were not masked, and the endpoint relies on pain-intensity reporting. This does not show that the outcome is biased, but awareness of assignment is a relevant possibility when assessing subjective measures. The record does not provide details on safeguards, missing-data handling, or sensitivity analyses that would help evaluate these concerns.

The posted secondary full-responder findings do not remove the primary endpoint uncertainty. The record does not report a multiplicity approach, and the secondary analyses are unadjusted. The most defensible conclusion is descriptive: the recorded counts and estimates do not show a precise, clearly separated pattern in non-responder risk across the comparisons, while the confidence intervals leave room for differences that the study results do not resolve. This is a statistical interpretation of posted data, not medical advice or a recommendation about treatment.

17. Why This Trial Matters Statistically

This trial is statistically interesting because it compares four active opioid strategies in a randomized parallel design, while the posted primary endpoint is a binary classification based on pain reports. The setup illustrates how a clinically meaningful question can produce estimates that remain uncertain when event counts are limited. A point estimate gives a concise summary, but the confidence interval shows how much more or less difference the data can still accommodate.

The study also illustrates why statistical non-significance and equivalence are not the same conclusion. Each primary interval includes zero, yet the intervals also include nonzero differences. Without a prespecified equivalence or non-inferiority framework, the result cannot be treated as evidence that the strategies have the same effect. The absence of a clear difference in these data is not a precise estimate of sameness.

Another statistical lesson is the importance of outcome definitions. Classifying participants as non-responders or full responders simplifies presentation but leaves out the detail in continuous pain scores and any intermediate categories. The registry does not report analyses of the full pain-score distribution or details on how response categories relate to each other. The reported counts answer a narrower question than the broader clinical description of analgesic efficacy.

Finally, the record shows why interpretation depends on reporting as well as design. The randomized, intention-to-treat labels are informative, but missing-data methods, the original sample-size justification, multiplicity handling, and other protocol-level analysis choices are not reported in the registry record. Those omissions limit what can be concluded from the posted estimates and make transparent reporting an important part of statistical evaluation.

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.

Several limitations are specific to the available record. The trial was unmasked, while the primary endpoint depends on reported pain intensity. Awareness of assigned strategy could potentially influence reporting or care decisions, although the record does not show whether or how much this occurred. No details are reported on procedures for standardized assessment or on steps taken to reduce expectation-related effects.

The endpoint is a binary classification at 28 days. It does not show the full distribution of pain scores, the size of change for each participant, or the timing of changes during follow-up. The registry description mentions dose increases, switching, and permanent treatment abandonment as topics of interest, but results for these outcomes are not reported in the available record. Thus, the posted result does not represent the full set of treatment experiences described in the study rationale.

Participant flow, missing outcome counts, and the handling of missing values are not reported. Although the primary population is labeled intention-to-treat, the operational approach cannot be evaluated from the registry record. The record also does not describe adherence, treatment exposure, protocol deviations, baseline characteristics, or reasons for withdrawal. These details would help assess comparability after randomization and the interpretation of outcome counts.

The reported primary comparisons are unadjusted, and the record does not state whether multiplicity was controlled. It also does not report the statistical method used to construct confidence intervals, a protocol-level analysis plan, or the trial’s own original sample-size assumptions. The planning illustrations are not a substitute for that information. These limitations apply to interpretation of the registry results and should not be taken as evidence that any particular bias or analysis problem occurred.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: RCT Comparing the Analgesic Efficacy of 4 Therapeutic Strategies Based on 4 Different Major Opioids (Fentanyl, Oxycodone, Buprenorphine vs Morphine) in Cancer Patients With Moderate/Severe Pain, at the Moment of Starting 3rd Step of WHO Analgesic Ladder. — NCT01809106.
• Registry record last updated 2015-12-24; status last verified 2015-10.
• Results first posted 2015-11-20.
• 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 completed Phase 4, randomized, unmasked, parallel-group trial enrolling 518 participants with cancer pain. It compares morphine with oxycodone, buprenorphine, and fentanyl. The primary endpoint is the number of intention-to-treat participants classified as non-responders at 28 days.

Primary non-responder counts were 14 of 122 for morphine, 18 of 125 for oxycodone, 14 of 127 for buprenorphine, and 11 of 124 for fentanyl. Each posted unadjusted risk-difference interval includes zero and spans differences in either direction. The record also posts full-responder counts and selected secondary comparisons, alongside descriptive adverse-event counts.

Important details, including the trial’s original sample-size justification, missing-data methods, multiplicity approach, and protocol-level analysis plan, are not reported in the registry record. The estimates are best interpreted with their uncertainty and the limitations of the available reporting in mind.