A Two-Part Study of Sativex® Oromucosal Spray for Relieving Uncontrolled Persistent Pain in Patients With Advanced Cancer: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Two-Part Study of Sativex® Oromucosal Spray for Relieving Uncontrolled Persistent Pain in Patients With Advanced Cancer (NCT01424566), a randomized phase 3 study. The primary outcome is Change From Randomization Baseline In Mean NRS Average Pain At End Of Treatment.

2. Clinical Question

The clinical question concerns persistent average pain in a population whose pain remained uncontrolled despite optimized opioid therapy. It is not a question about breakthrough pain, nor does the primary endpoint directly measure every aspect of cancer-related symptoms, function, or quality of life. The registry describes nabiximols as adjunctive therapy, so the comparison concerns adding the study spray in the setting of ongoing care rather than replacing existing treatment.

The registry record describes a two-part study in which all enrolled participants received nabiximols during one of the parts, without knowing which part. The randomized comparison of double-blind nabiximols with double-blind placebo addresses the primary question. The trial enrolled 406 participants overall, while the posted primary outcome results report 103 in each randomized group. The registry does not report enough detail to infer how every enrolled participant proceeded through both parts or why the primary analysis population differs from the overall enrollment.

3. Trial Design

This was a phase 3, randomized, triple-masked, parallel-group study sponsored by Jazz Pharmaceuticals. The registry record describes a multicenter, two-part study of nabiximols as adjunctive therapy for persistent pain in advanced cancer. The study status is completed. Overall enrollment was 406; the posted primary outcome analysis includes 103 participants in the double-blind nabiximols group and 103 in the double-blind placebo group.

The study design included a single-blind nabiximols part and a double-blind randomized comparison. The record says all participants enrolled in the trial received nabiximols during one of the two parts, but did not know which part. It also says participants were not required to discontinue their current treatments or medications. These details mean that the posted randomized comparison is not a comparison of nabiximols against withdrawal of usual care: placebo was the assigned study spray, alongside ongoing treatment as applicable.

The intervention descriptions specify morning and evening self-administration, a maximum of 10 sprays per day, and different listed treatment durations: 2 or 7 weeks for nabiximols and 5 weeks for placebo. The primary endpoint timeframe is randomization baseline to end of treatment, identified as Day 36 of the double-blind period. The registry record does not report the reasons for the listed differences in durations or further detail about how the two-part sequence was managed.

Triple masking means that the registry identifies the study as masked at multiple levels, but the specific roles masked are not reported in the registry record. The allocation ratio, randomization method, and detailed concealment procedures are also not reported in the registry record. These design features matter when assessing the risk of bias, but their absence from the record does not establish that a particular procedure was or was not used.

The primary analysis population was defined as participants who were randomized, received at least one dose of study drug, and had at least one efficacy endpoint. They were analyzed according to randomized treatment assignment. This is the population described for the primary efficacy endpoint; it should not be confused with the overall enrollment count or with the separate safety groups.

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: Per the Statistical Analyses Plan, all randomized participants who received at least 1 dose of study drug were analyzed in the Intent to Treat (ITT) population as per randomized treatment group. Participants were included and analyzed according to the treatment group they were randomized to.

Single-blind Treatment

Reasons for not completing this period:

Double-blind Treatment

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The ITT Population included all participants who were randomized, received at least 1 dose of study drug, and had at least 1 efficacy endpoint. Participants were analyzed according to the treatment group they were randomized to.

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.

Population: All participants who were randomized and received at least 1 dose of study drug. Two participants who were randomized in the single-blind treatment period did not administer any study drug.

6. Primary Endpoint

The registry lists the primary outcome as Change From Randomization Baseline In Mean NRS Average Pain At End Of Treatment, measured over Randomization Baseline, End of Treatment (Day 36 of the double-blind period).

The primary endpoint was change from randomization baseline in mean average pain at end of treatment. Participants reported pain experienced during the last 24 hours using an 11-point numerical rating scale, ranging from 0 for no pain to 10 for pain as bad as can be imagined. The endpoint is a continuous measure: each participant’s change was calculated as the end-of-treatment score minus the randomization baseline score.

The baseline was the mean of the last 4 consecutive days of the single-blind treatment period, before randomization in Part B. A negative change indicates improvement in average pain from that baseline; a positive change indicates a higher pain score at end of treatment. The treatment comparison therefore concerns the mean change between randomized groups, rather than the end-of-treatment score alone or the proportion of participants who improved.

Average pain is used because it provides a repeated, patient-reported measure of pain intensity over a stated recall period. Comparing change from baseline can describe how scores moved during the double-blind treatment period while taking the starting score into account. General statistical context: a mean summarizes the group’s average change, but does not show how much individual participants varied or how many experienced a particular degree of improvement. The reported standard deviations provide information about variability, while the group comparison and its confidence interval address uncertainty about the difference in mean change.

The endpoint is specific to average pain over the preceding 24 hours. It does not by itself establish effects on breakthrough pain, sleep, opioid use, satisfaction, or other outcomes. Those topics appear among the registry’s secondary outcomes and require separate interpretation.

7. Results Posted in the Registry

• Double-blind Nabiximols: mean 0.50 versus 0.50 on control; difference 0.00 (95% CI -0.40 to 0.40), standardized effect d = 0.00; z-test p = 1.000.

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.

Change From Randomization Baseline In Mean NRS Worst Pain At End Of Treatment

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Double-blind Nabiximols: mean 0.20 versus 0.50 on control; difference -0.30 (95% CI -0.71 to 0.11), standardized effect d = -0.20; z-test p = 0.152.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Double-blind Nabiximols and the control. The interval gives the range of effects that remain compatible with the data.

Change From Randomization Baseline In Mean Sleep Disruption NRS At End Of Treatment

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Double-blind Nabiximols: mean 0.20 versus 0.50 on control; difference -0.30 (95% CI -0.67 to 0.07), standardized effect d = -0.22; z-test p = 0.111.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Double-blind Nabiximols and the control. The interval gives the range of effects that remain compatible with the data.

Change From Randomization Baseline In Daily Total Opioid Use (Morphine Equivalent) At End Of Treatment

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Double-blind Nabiximols: mean 9.00 versus 15.50 on control; difference -6.50 (95% CI -23.60 to 10.60), standardized effect d = -0.10; z-test p = 0.456.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Double-blind Nabiximols and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists secondary outcomes covering worst pain, sleep disruption, patient and physician impressions of change, satisfaction, and opioid use. This breadth provides context beyond the primary average-pain measure, but the outcomes do not all capture the same construct. Patient-reported ratings, global impressions, satisfaction, and medication-use measures each answer different questions.

Among the quantitative secondary comparisons with posted group summaries, the estimated differences are in the direction of lower change in the nabiximols group. Their confidence intervals include zero, and the reported unadjusted p-values do not provide clear evidence of a group difference. The opioid-use comparison is also uncertain, with its interval spanning values in either direction. Taken together, these results do not provide a clear secondary-outcome pattern that overturns or materially strengthens the primary finding.

This is an overall reading of the posted quantitative comparisons, not a substitute for interpreting each outcome on its own scale. A lower change can have different meanings depending on whether the measure is pain, sleep disruption, or opioid use. The global impression and satisfaction outcomes are listed in the registry, but the numerical results for those measures are not included in the registry record for this interpretation; their direction and precision are therefore not reported in the registry record.

Unadjusted secondary results carry less weight because examining multiple outcomes creates more opportunities for an apparently notable result to arise by chance, even when there is no underlying effect. General statistical context: multiplicity procedures can control the overall error rate across a family of tests, but the registry record does not report whether such procedures were planned or applied to these secondary outcomes. A collection of separate unadjusted p-values should not be treated as if each were the sole prespecified test. These secondary findings are best considered supportive or exploratory unless a fuller analysis plan establishes their confirmatory role.

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

• Percent Improvement From Eligibility Baseline In Mean NRS Average Pain Score At End Of Treatment
• Change From Randomization Baseline In Mean NRS Worst Pain At End Of Treatment
• Change From Randomization Baseline In Mean Sleep Disruption NRS At End Of Treatment
• Subject Global Impression Of Change At Last Visit (Up To Day 36 Of The Double-blind Period)
• Physician Global Impression Of Change At Last Visit (Up To Day 36 Of The Double-blind Period)
• Patient Satisfaction Questionnaire At Last Visit (Up To Day 36 Of The Double-blind Period)
• Change From Randomization Baseline In Daily Total Opioid Use (Morphine Equivalent) At End Of Treatment
• Change From Randomization Baseline In Daily Maintenance Opioid Dose (Morphine Equivalent) At End Of Treatment

9. Statistical Interpretation

10. Statistical Methods Explained

What does the mean difference represent?

The primary measure is continuous, and the registry reports a mean and standard deviation for each randomized group. The mean is the arithmetic average of participants’ changes from baseline. The primary comparison asks whether that average change differed between double-blind nabiximols and placebo. In the posted group summaries, both means are 0.5; the unadjusted recalculation from those summaries is 0.0. This is a comparison of group averages, not a count of participants who improved or worsened.

General statistical context: a mean difference is easiest to interpret when the outcome’s direction is clear. Here, negative changes indicate improvement, so a negative difference in change would indicate a lower average change in the nabiximols group than in placebo. That direction alone does not establish clinical importance. The size of a difference must be considered alongside the scale, uncertainty, and a clinically meaningful threshold. Such a threshold is not reported in the registry record.

What is the role of the standard deviation?

The standard deviation describes the spread of individual observations around a group mean. It is not the standard error of the mean and it is not a confidence interval. The primary outcome standard deviations are 1.3 for nabiximols and 1.6 for placebo. The posted group summaries therefore indicate variation among participants’ changes within each group, even though the rounded group means are equal.

General statistical context: variability affects the precision of a group mean and the comparison between groups. Greater spread generally makes it harder to estimate a mean difference precisely when other design features are held constant. A group mean can conceal a range of individual responses; the mean and standard deviation do not show the full shape of the outcome distribution or the number of participants at any particular response level.

Why are there two versions of the primary comparison?

The registry reports a sponsor analysis using ANCOVA, with a mean difference of -0.02, a 95% confidence interval from -0.42 to 0.38, and p = 0.917. ANCOVA is a method for comparing outcomes while adjusting for specified covariates. The registry record does not report the full model specification, so the adjustment cannot be reproduced from the posted summary statistics alone.

The simple recalculation uses the posted group means and standard deviations to estimate an unadjusted difference and its uncertainty. It is descriptive of the summary data and does not use the sponsor’s model adjustments. Differences between an adjusted and unadjusted estimate can arise because they answer the comparison using different statistical procedures; the estimates should not be treated as interchangeable. The sponsor’s reported analysis is the registry’s own inferential analysis, while the recalculation is a separate summary-statistics-based check.

What does the confidence interval add?

A point estimate gives one value for the estimated difference, while a confidence interval expresses the uncertainty around that estimate. General statistical context: under the analysis assumptions, intervals constructed by the same procedure over repeated studies would contain the underlying parameter at the stated rate. A confidence interval is not a range containing a stated percentage of individual participant outcomes, and it is not a probability statement about the fixed treatment effect after observing the data.

For the sponsor’s primary analysis, the interval ranges from -0.42 to 0.38 and includes zero. The recalculated interval also includes zero. Thus, both analyses leave uncertainty about the direction of the group difference. The interval width matters as well as whether zero is included: a broad interval allows a wider range of possible effects than a narrow one. The registry record does not report a clinical threshold against which that range could be judged.

What can a p-value say?

The sponsor’s ANCOVA p-value is 0.917, while the unadjusted recalculation gives p = 1.0. A p-value is calculated under a statistical model that specifies a null hypothesis, here a no-difference comparison, and depends on the method and its assumptions. It describes how compatible the observed data are with that null model; it is not the probability that the null hypothesis is true, nor the probability that the observed result arose by chance in an everyday sense.

The two p-values are associated with different analyses, so their numerical difference should not be interpreted as conflicting evidence. Both are consistent with the corresponding estimates and confidence intervals that include zero. The registry record does not report a prespecified significance threshold for the primary analysis, though a two-sided significance level of 0.05 is stated among the assumptions for planning illustrations. Those planning assumptions should not be mistaken for the primary analysis plan.

How should the planning illustrations be read?

The sample-size planning illustrations use the observed effect, a two-sided significance level of 0.05, equal allocation, and a normal approximation. They display the participants per arm that would be needed to detect stated fractions of the observed effect under those assumptions. These are planning illustrations based on the observed result, not the trial’s original sample-size justification and not observed power.

General statistical context: planning estimates depend strongly on the effect chosen for detection and on the variability assumed. Smaller target effects generally require larger planned samples for a given power target. Because the effect is taken from the observed comparison, the illustrations are not independent evidence about whether the intervention has an effect. The trial’s own sample-size justification and the assumptions used in its original design are not reported in the registry record.

For continuous outcomes, the planning illustrations report participants per arm. They should be used as hypothetical design aids, not as a post hoc scorecard for the completed trial. In particular, an observed p-value cannot be converted into observed power to determine whether a study “had enough power.” The relevant interpretation remains the estimated effect, its uncertainty, the analysis method, and the quality and completeness of the outcome data.

11. Confidence Intervals and Precision

Precision concerns how much uncertainty surrounds an estimated difference. For the primary endpoint, the sponsor’s ANCOVA estimate was -0.02, with a 95% confidence interval from -0.42 to 0.38. The interval includes zero and allows for values on either side of no difference. The posted unadjusted recalculation also has a confidence interval that includes zero. Both results therefore leave uncertainty about the direction and size of the group difference.

The sponsor’s interval is expressed in units on the average-pain scale. Its limits indicate that the data and model are compatible with a range of differences, not that every value in that range is equally likely or that the true difference has a 95% probability of lying within the observed interval. General statistical context: a confidence interval quantifies sampling uncertainty under the model and assumptions used to construct it. It does not incorporate every source of uncertainty, such as possible measurement limitations, missing data, or departures from the analysis assumptions.

The primary randomized groups each have 103 participants in the posted outcome results. The sponsor’s analysis and the simple recalculation use different methods, so their intervals need not match exactly. The registry record does not report the model details needed to reproduce the ANCOVA interval, nor does it report a clinically important difference threshold. Consequently, the interval can be read statistically as including no difference, but its clinical implications cannot be calibrated against a registry-reported threshold.

Precision is distinct from whether a result is statistically significant. An estimate close to zero with an interval that crosses zero does not prove equivalence or establish that any possible difference is negligible. Equivalence or non-inferiority would require a prespecified margin and an appropriate analysis; such a margin is not reported in the registry record. The result is best read as an estimate with uncertainty rather than a definitive demonstration of identical effects.

12. Analyses Reported by the Sponsor

The sponsor’s reported primary analysis used ANCOVA and estimated a mean difference of -0.02 in average-pain change, with a 95% confidence interval from -0.42 to 0.38 and p = 0.917. The confidence interval includes zero. The posted group means are both 0.5, and the simple unadjusted recalculation from those summaries gives a difference of 0.0, with an interval that also includes zero and an unadjusted p-value of 1.0.

The two estimates are close in point value and support the same broad reading: the posted primary results do not show a clear difference in mean change between randomized groups. They are not identical analyses. ANCOVA adjusts according to a model, while the recalculation uses posted summary statistics without those model adjustments. The registry record does not report enough detail about the ANCOVA specification to reproduce the sponsor’s estimate.

The sponsor analysis should be read as the trial’s reported inferential analysis. The recalculation is a transparent, unadjusted comparison of the posted summaries, not a replacement for the sponsor’s model or an independent reanalysis of participant-level data. The registry record marks no discrepancy between the sponsor analysis and the recalculation. Neither analysis establishes equivalence, and the record does not report a clinical importance threshold for judging the full range of differences compatible with the confidence intervals.

13. Multiplicity, Missing Data and Analysis Populations

The registry record lists one primary analysis and 10 posted secondary outcomes. It reports a sponsor ANCOVA for the primary endpoint, but does not report whether the secondary outcomes were arranged into prespecified families, whether a hierarchy was used, or whether p-values were adjusted for multiple testing. The multiplicity plan is therefore not reported in the registry record.

General statistical context: when several outcomes or comparisons are examined, the chance of at least one apparently unusual result can increase. An adjustment or prespecified testing sequence can address this issue, but it may also affect the interpretation and precision of individual tests. Without a reported plan, the secondary p-values should be treated cautiously and should not be read as a set of independent confirmatory findings. This limitation does not change the numerical values; it affects how much evidential weight they can carry.

The primary analysis population is described as randomized participants who received at least one dose and had at least one efficacy endpoint, analyzed according to randomized assignment. This definition gives useful information about who was included, but the registry record does not report the number excluded from the primary analysis, reasons for exclusion, or the amount and pattern of missing endpoint data. The handling of missing outcomes, including any imputation or sensitivity analyses, is not reported in the registry record.

General statistical context: missing data can affect results if the likelihood of an outcome being observed is related to the outcome itself or to treatment assignment. The direction and size of any resulting bias cannot be determined from a population definition alone. The primary population also excludes randomized participants who did not meet its dose and endpoint requirements, so the analysis does not simply represent every person enrolled. The registry record does not report enough detail to assess how these exclusions might affect the comparison.

The protocol’s sample-size justification, interim-analysis plan, and detailed statistical analysis plan are not reported in the registry record. The posted planning illustrations are based on the observed effect and specified hypothetical assumptions; they do not fill that gap or establish the trial’s original design rationale. These omissions limit assessment of prespecification and analysis choices, while leaving the posted estimates and their stated methods interpretable on their own terms.

14. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: neoplasm progression (27.2%), anaemia (1.9%), cancer pain (1.0%), gastrointestinal haemorrhage (1.0%), cellulitis (1.0%).

The registry reports serious adverse events and other adverse events separately for the single-blind and double-blind groups. In the double-blind groups, serious adverse events affected 33 participants in the nabiximols group and 16 in the placebo group; the registry lists 103 participants at risk in each group. Other adverse events affected 21 participants in the double-blind nabiximols group and 17 in the double-blind placebo group. These are reported counts, not adjusted comparisons.

For the single-blind nabiximols group, the registry lists 80 participants affected by serious adverse events and 97 affected by other adverse events, with 404 at risk for each category. Serious-event terms listed include Neoplasm Progression at 27.2%, as well as Anaemia at 1.9%, and Cancer Pain, Gastrointestinal Haemorrhage, Cellulitis, and Pneumonia at 1.0% each. Deaths are not reported in the registry record.

These figures require caution. The record presents separate study groups and does not provide an adjusted safety comparison or detail sufficient to interpret differences as causal. The study’s two-part structure and the listed treatment periods also mean the group counts should not be treated as a complete account of comparable exposure without further information. The serious-event listings describe reported safety experience; they do not alone determine the balance of benefits and risks.

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

The primary result is an estimate of the difference between randomized groups in mean change in average pain from the Part B randomization baseline to end of treatment. The posted means were 0.5 in both groups, and the sponsor’s ANCOVA estimate was -0.02. The sponsor’s confidence interval included zero, as did the interval from the unadjusted recalculation. The registry record therefore does not show a clear difference between the groups on this primary measure.

That conclusion is narrower than saying that nabiximols has no effect, or that it cannot help any participant. Group averages can conceal varied individual experiences, and a confidence interval that includes zero does not prove that the true difference is exactly zero. Nor does this result establish that nabiximols and placebo are equivalent: an equivalence conclusion would require a prespecified margin and a suitable analysis, and no such margin is reported in the registry record.

The result also does not answer every question about pain care in advanced cancer. The endpoint concerns average pain over the last 24 hours, measured on an 11-point scale, during the stated study period. It is not a direct result for breakthrough pain, long-term use, or every listed secondary outcome. Participants were not required to stop their current treatments or medications, so the study question concerns adjunctive use in the context of ongoing care as described in the registry.

General statistical context: statistical uncertainty and clinical importance are related but distinct. A confidence interval can show which differences are compatible with the data under an analysis, but a clinical threshold is needed to judge whether those differences would matter to patients or clinicians. The registry record does not report such a threshold for the primary endpoint. The result should therefore be read as evidence about the estimated group contrast and its precision, not as a complete judgment about clinical value.

Finally, interpretation depends on the analyzed population and the completeness of the endpoint data. The primary population required randomization, at least one dose, and at least one efficacy endpoint. The registry does not report detailed missing-data handling or the reasons for exclusions from that population. Those gaps do not invalidate the reported comparison, but they limit the assessment of how robust it is to missingness and analysis choices.

16. Why This Trial Matters Statistically

This trial illustrates why a clinical result should be read through its endpoint definition before interpreting the numbers. The primary measure was change in average pain, and its sign has a specific meaning: negative values indicate improvement from baseline. Without that definition, a positive mean change or a negative between-group estimate could easily be misread.

It also shows the value of separating an adjusted sponsor analysis from an unadjusted recalculation. The ANCOVA estimate and the summary-statistics-based estimate are close to zero, but they arise from different methods. The recalculation helps readers understand the posted group means and variability; it cannot recreate a model whose specification is not reported. The comparison reinforces that a numerical result depends on both the data and the analysis method.

Precision is another central issue. The primary interval includes zero, so the point estimate alone should not be treated as a definitive answer. At the same time, an interval that includes zero does not prove that the groups are identical. Without a clinical importance threshold, it is not possible to say from the registry record whether every difference still compatible with the data would be unimportant.

The secondary outcomes show why multiplicity matters in clinical research. Multiple symptom, impression, satisfaction, and medication-use outcomes can add perspective, but separate unadjusted findings need cautious interpretation. A clearly reported analysis plan is needed to distinguish confirmatory outcomes from exploratory ones. The registry record does not report whether secondary testing was adjusted or organized hierarchically.

Finally, the registry’s analysis-population definition and limited missing-data detail matter for judging the reach of the result. The primary estimate applies to the defined efficacy population, not automatically to every enrolled participant. Together, these issues make the trial statistically informative while also identifying what cannot be established from the registry record alone.

17. Limitations

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

The registry record leaves several trial-specific details unavailable. It does not report the randomization procedure, allocation ratio, the roles covered by triple masking, or the detailed sequence and conduct of the two study parts. The record says participants received nabiximols during one of the two parts without knowing which part, but does not provide enough information to reconstruct the experience of every participant or the transition between parts.

The listed treatment periods differ: the nabiximols description gives 2 or 7 weeks, while the placebo description gives 5 weeks. The primary outcome is framed at end of treatment and identified as Day 36 of the double-blind period. The registry does not explain the differing durations, so they should not be used to infer treatment exposure for individual participants or to make unreported comparisons of exposure.

The primary efficacy analysis includes randomized participants who received at least one dose and had at least one efficacy endpoint. The registry does not report detailed participant flow into that population, reasons for exclusions, missing outcome counts, or missing-data methods. It also does not report sensitivity analyses addressing missingness. These omissions limit assessment of potential bias from incomplete outcome data.

The sponsor reports ANCOVA, but the model specification and covariates are not reported in the registry record. The protocol’s sample-size justification, original design assumptions, interim-analysis plan, and full statistical analysis plan are also not reported. The planning illustrations based on observed effects are not a substitute for those design details.

The clinical meaning of the primary estimate is difficult to calibrate without a reported threshold for a clinically important difference. The posted results focus on mean change, which does not describe individual response patterns. Secondary outcomes broaden the scope but include measures with different meanings, and the registry record does not report a multiplicity strategy. These limitations call for a measured interpretation of the estimates rather than a categorical conclusion about all outcomes or all participants.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: A Two-Part Study of Sativex® Oromucosal Spray for Relieving Uncontrolled Persistent Pain in Patients With Advanced Cancer — NCT01424566.
• Registry record last updated 2023-04-12; status last verified 2023-04.
• Results first posted 2018-04-23.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

21. Record Summary

NCT01424566 is a completed phase 3 randomized, triple-masked, parallel-group study sponsored by Jazz Pharmaceuticals. It evaluated adjunctive nabiximols versus placebo for uncontrolled persistent chronic pain in participants with advanced cancer who had inadequate analgesia despite optimized chronic opioid therapy. Overall enrollment was 406.

The primary endpoint was change from randomization baseline in mean average-pain score at end of treatment, measured on an 11-point numerical rating scale. The posted group means were 0.5 for double-blind nabiximols and 0.5 for double-blind placebo, with 103 participants in each group. The sponsor’s ANCOVA estimate was -0.02, with a 95% confidence interval from -0.42 to 0.38 and p = 0.917. The interval includes zero; the unadjusted recalculation is also centered near no difference.

The record lists secondary outcomes for pain, sleep disruption, global impressions, satisfaction, and opioid use. Multiplicity procedures, detailed missing-data handling, the full ANCOVA specification, and the protocol’s sample-size justification are not reported in the registry record. The posted findings are most appropriately interpreted as uncertain estimates for the defined outcomes and analysis population, not as proof of equivalence or a universal treatment effect.