Assessment of Efficacy and Safety in Patients With Non-cancer-related Pain and Opioid-induced Constipation: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Assessment of Efficacy and Safety in Patients With Non-cancer-related Pain and Opioid-induced Constipation (NCT01323790), a randomized phase 3 study. The primary outcome is Response (Responder/Non-responder) to Study Drug During Weeks 1 to 12.

2. Clinical Question

3. Trial Design

The registry describes NCT01323790 as a Phase 3, randomized, double-blind, placebo-controlled study. Its official title identifies a triple-masked, parallel-group design. The interventions were oral NKTR-118 at 12.5 mg, oral NKTR-118 at 25 mg, and oral placebo. The registry records enrollment as 700 and status as completed. The study start is listed as 2011-03 and primary completion as 2012-09.

The stated purpose was to evaluate the effect and safety of NKTR-118 in patients with opioid-induced constipation and non-cancer-related pain, including patients with an inadequate response to laxative therapy. The primary outcome was a binary responder/non-responder measure over the treatment period. The posted primary outcome counts were 81 of 232 for NKTR-118 12.5 mg, 92 of 232 for NKTR-118 25 mg, and 68 of 232 for placebo. These are the registry’s posted arm summaries; they should not be confused with the enrollment figure.

The ITT analysis set is described as including all randomized patients except those found to have been randomized multiple times within the program at different centers. The registry does not report further detail about how randomization was generated, whether allocation was stratified, or which individuals were masked. Those aspects are not reported in the registry record. The registry lists 11 outcome measures and 24 analyses, while outcome-specific analysis details vary. The study’s original design assumptions and any sample-size justification 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.

Before assignment: The study duration was up to 18 weeks, consisting of an initial screening period lasting up to 2 weeks, a 2-week OIC confirmation period, during which the diagnosis of OIC and stability of the opioid regimen were confirmed, a 12-week treatment period, and a follow-up visit 2 weeks after the last dose of study drug.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The ITT analysis set included all randomized patients, with the exception of patients who were found to have randomized multiple times within the program at different centers.

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: A total of 4 patients (2 patients in the NKTR-118 25 mg and 1 patient each in the NKTR-118 12.5 mg and placebo groups) had been previously randomized within the NKTR-118 program at a different study center. These patients were excluded from the ITT and Safety analysis sets. Baseline characteristics are summarized based on the ITT analysis set.

6. Primary Endpoint

The registry lists the primary outcome as Response (Responder/Non-responder) to Study Drug During Weeks 1 to 12, measured over Baseline (Week 1) to end of treatment (Week 12).

The primary endpoint classifies each patient as a responder or non-responder during Weeks 1 to 12. The definition combines a minimum weekly frequency of spontaneous bowel movements with an improvement over baseline, and requires that these conditions be met over much of the treatment period, including the final weeks. A spontaneous bowel movement is one occurring 24 hours or more after the last use of rescue medication. This definition therefore distinguishes spontaneous bowel movements from bowel movements that occur soon after rescue medication.

A binary endpoint is useful when the clinical question is whether patients achieve a prespecified response criterion, rather than how much an average measurement changes. It gives a direct count of patients meeting the definition in each arm and supports comparisons of response probabilities. The trade-off is that a responder threshold compresses information: patients just meeting the criterion and patients exceeding it are both counted as responders, while patients just short of it and those far below it are both counted as non-responders.

The endpoint is not a measure of every aspect of constipation or of safety. The registry separately lists secondary outcomes, including bowel-movement frequency, straining, stool consistency, and time to first post-dose laxation. The response definition and its observation period are stated in the registry; further details about handling incomplete endpoint data are not reported in the registry record.

7. Results Posted in the Registry

• NKTR-118 12.5 mg: 34.9% (81/232) versus 29.3% (68/232) on control; risk difference 5.6 percentage points (95% CI -2.9 to 14.1), risk ratio 1.19 (0.91–1.55); unadjusted two-proportion z-test p = 0.196.
• NKTR-118 25 mg: 39.7% (92/232) versus 29.3% (68/232) on control; risk difference 10.3 percentage points (95% CI 1.7 to 18.9), risk ratio 1.35 (1.05–1.75); unadjusted two-proportion z-test p = 0.019.

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.

Response (Responder/Non-responder) to Study Drug in the LIR Subgroup During Weeks 1 to 12

• 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:
  • NKTR-118 12.5 mg: 42.4% (53/125) versus 31.4% (38/121) on control; risk difference 11.0 percentage points (95% CI -1.0 to 23.0), risk ratio 1.35 (0.97–1.88); unadjusted two-proportion z-test p = 0.074.
  • NKTR-118 25 mg: 46.8% (58/124) versus 31.4% (38/121) on control; risk difference 15.4 percentage points (95% CI 3.3 to 27.4), risk ratio 1.49 (1.08–2.06); unadjusted two-proportion z-test p = 0.014.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between NKTR-118 12.5 mg 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 higher for NKTR-118 25 mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Change From Baseline in Mean Number of Days Per Week With at Least 1 SBM During Weeks 1 to 12

• 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 errors.
• Result:
  • NKTR-118 12.5 mg: mean 2.12 versus 1.73 on control; difference 0.39 (95% CI 0.06 to 0.72), standardized effect d = 0.21; z-test p = 0.022.
  • NKTR-118 25 mg: mean 2.41 versus 1.73 on control; difference 0.68 (95% CI 0.33 to 1.03), standardized effect d = 0.36; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for NKTR-118 12.5 mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for NKTR-118 25 mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Change From Baseline in Degree of Straining

• 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 errors.
• Result:
  • NKTR-118 12.5 mg: mean -0.67 versus -0.48 on control; difference -0.19 (95% CI -0.36 to -0.02), standardized effect d = -0.21; z-test p = 0.025.
  • NKTR-118 25 mg: mean -0.80 versus -0.48 on control; difference -0.32 (95% CI -0.49 to -0.15), standardized effect d = -0.35; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for NKTR-118 12.5 mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for NKTR-118 25 mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registry lists a range of secondary outcomes, including response in the LIR subgroup, time to first post-dose laxation, bowel-movement frequency, straining, stool consistency, and measures of complete or spontaneous bowel movements. Several posted results use different outcome scales and analysis methods. Taken as a group, the secondary outcomes provide additional descriptions of bowel-related measures and of the subgroup identified as having an inadequate response to laxative therapy.

The general pattern of posted secondary findings is compatible with the primary outcome’s focus on response and bowel-movement activity, but the outcomes do not all measure the same construct. A change in a continuous measure, a time-to-event measure, and a binary responder classification each answers a different question. The secondary outcomes can add context to the primary endpoint, but they should not be treated as interchangeable confirmations of it.

There are numerous outcomes and analyses in the registry record. When many comparisons are made, the chance of seeing some apparently notable results by chance can increase. Unadjusted secondary p-values do not account for that multiplicity unless an adjustment is explicitly applied. The registry does not report whether multiplicity was controlled or how the outcomes were prioritized. Consequently, secondary results carry less inferential weight than a clearly prespecified primary analysis, and individual secondary p-values are best viewed as exploratory unless the registry reports a confirmatory plan.

The posted secondary results also depend on the analysis methods and populations used for each outcome. Details such as missing-data assumptions, model specifications, and multiplicity procedures are not reported in the registry record. These reporting gaps limit how confidently the secondary findings can be compared or combined into a single overall conclusion.

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

• Response (Responder/Non-responder) to Study Drug in the LIR Subgroup During Weeks 1 to 12
• Time (in Hours) to First Post-dose Laxation Without the Use of Rescue Laxatives Within the Previous 24 Hours
• Change From Baseline in Mean Number of Days Per Week With at Least 1 SBM During Weeks 1 to 12
• Change From Baseline in Degree of Straining
• Change From Baseline in Stool Consistency (Bristol Stool Scale)
• Change From Baseline in Percent Numbers of Days With a CSBM (Complete Spontaneous Bowel Movement)
• Change From Baseline in Mean Spontaneous Bowel Movements/Week
• Time (in Hours) to First Post-dose Laxation Without the Use of Rescue Laxatives Within the Previous 24 Hours in the Laxative Inadequate Response (LIR) Subgroup

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary: each patient is classified as a responder or non-responder using the registry’s stated criteria. A comparison of binary outcomes can be expressed in different ways. The sponsor reported risk ratios from a Cochran-Mantel-Haenszel analysis, while the posted recalculations express the same arm summaries as risk differences. These measures answer related but distinct questions. A risk ratio compares the response probabilities as a ratio; a risk difference expresses their absolute separation on the probability scale. Neither measure should be substituted for the other without identifying which is being discussed.

The sponsor’s reported primary analyses used the Cochran-Mantel-Haenszel method. In general, this method can combine comparisons across strata while accounting for the stratification structure used in an analysis. The registry identifies the method but does not report the strata or enough detail to reconstruct the complete model. Its reported risk ratios and confidence intervals should therefore be read as the sponsor’s analysis, not as a result that can be fully recreated from the arm totals alone.

The recalculated binary comparisons are unadjusted calculations from the posted event counts and arm sizes. They do not reproduce the sponsor’s Cochran-Mantel-Haenszel analysis. Differences between an unadjusted calculation and a sponsor analysis can arise because the analyses use different methods or account for different structures in the data. The registry record flags a discrepancy, so the sponsor’s own analysis takes precedence. The recalculated results are useful as a transparent descriptive check, not as a replacement for the reported analysis.

A confidence interval gives a range of effect estimates compatible with the observed data under the model and method used. For a risk ratio, a value of 1 represents equal risks; for a risk difference, 0 represents no difference. Intervals spanning the corresponding null value include estimates consistent with no difference. An interval entirely on one side of that value indicates that the estimates covered by the interval are on that side, subject to the analysis assumptions. The interval does not capture every source of uncertainty, such as limitations in the registry’s reporting or possible bias.

The p-value describes how unusual results at least as incompatible with the null hypothesis would be if that hypothesis and the analysis assumptions held. It is not the probability that the null hypothesis is true, nor does it quantify the size or clinical importance of an effect. The registry reports p-values for the sponsor’s comparisons and the recalculations; the two sets should remain distinguished because they come from different analyses.

Several continuous secondary outcomes are reported as least-squares means with standard errors, and sponsor comparisons use mixed models analysis. In general, a least-squares mean is a model-based mean, and a mixed model can account for repeated measurements or other modeled data structure. The exact model specification, covariance assumptions, and missing-data assumptions are not reported in the registry record. The displayed recalculations for continuous outcomes use approximations based on the posted summaries; they are not a substitute for the mixed-model analyses reported by the sponsor.

Standard error describes the estimated sampling variability of a statistic, rather than the spread of individual patient measurements. A confidence interval based on a standard error reflects uncertainty in the estimated mean or contrast under the relevant method. The registry reports standard errors for the listed least-squares means, but does not provide all information needed to independently reproduce the sponsor’s model-based confidence intervals.

Over-dispersion is a general concern when variation in count or binary data is greater than the analysis model allows. If it is ignored, standard errors may be too small and intervals too narrow. It is not reported as an issue or adjustment in this registry record, so no conclusion about whether it affected these analyses can be drawn. Likewise, details of interim analyses, outcome hierarchy, or a prespecified statistical analysis plan are not reported in the registry record.

11. Confidence Intervals and Precision

The sponsor’s primary risk-ratio estimate for NKTR-118 12.5 mg versus placebo is 1.188, with a 95% confidence interval from 0.911 to 1.548. The interval includes 1, so the estimates compatible with the reported analysis include equal response risk as well as estimates on either side of equality. The p-value is 0.202. The interval is wide enough that the registry result does not identify a narrow range of relative effects.

For NKTR-118 25 mg versus placebo, the sponsor-reported estimate is 1.348, with a 95% confidence interval from 1.045 to 1.739. This interval is above 1, but still covers a range of possible relative differences. Its p-value is 0.021. A confidence interval provides information about precision as well as direction: an estimate alone does not convey how much uncertainty surrounds it.

The recalculated risk-difference intervals are -0.029 to 0.141 for 12.5 mg versus placebo and 0.018 to 0.189 for 25 mg versus placebo. These intervals are based on simple unadjusted recalculations and differ from the sponsor’s risk-ratio intervals in both effect measure and method. Since the registry record flags a discrepancy, the sponsor’s own analysis takes precedence for the trial’s reported inference.

In general, confidence intervals reflect sampling uncertainty under the specified analysis. They do not address every concern, including missing-data handling, multiplicity, selection of outcomes, or limitations in the registry record. The intervals should be interpreted alongside the analysis method and the fact that multiple outcomes and comparisons are listed.

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 observed effects, not the original trial design. For these binary outcomes, the figures are participants per arm. The registry’s sample-size assumptions specify a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is a stated fraction of the observed effect. The trial’s own original design assumptions and sample-size justification are not reported in the registry record.

The 80% power column gives the illustrative number of participants per arm for a hypothetical study to have an 80% chance of detecting the specified effect under the stated assumptions, if that effect and assumptions were correct. The 90% power column gives the corresponding number for a 90% chance. These are planning concepts: power is the probability of rejecting the null hypothesis under a specified alternative, not the probability that a result will be statistically significant after data are collected.

Rows using 100% of the observed effect use the observed effect as the hypothetical target. Rows using 75% or 50% of the observed effect consider smaller targets. Smaller effects are harder to distinguish from random variation, so they require more participants per arm to reach the same target power under the stated assumptions. The listed figures are not observed power; they are planning illustrations calculated from the observed effects.

These calculations are simplified and do not reproduce the trial’s original design process. Their results depend on the stated assumptions, including equal allocation, the normal approximation, and the chosen fraction of the observed effect. They should not be read as evidence that the study was designed or conducted using those assumptions.

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 = 0.293; treatment proportion p₁ = 0.349; average p̄ = 0.321.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6603 = 1.2942.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6591 = 0.5547.
4. n = (1.2942 + 0.5547)² / (0.0560)² = 1,088.7, rounded up to 1,089 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 <- 0.293103448275862                          # control proportion
p1 <- 0.349137931034483                          # 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(1323790)
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 = 1,089 (80% power), 1,457 (90% power)
 75% of observed effect: n per arm = 1,914 (80% power), 2,562 (90% power)
 50% of observed effect: n per arm = 4,255 (80% power), 5,695 (90% power)
power.prop.test: 1088.7 
Simulated power at n = 1,089 per arm: 0.800 (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. Analyses Reported by the Sponsor

The registry reports the sponsor’s primary comparisons as Cochran-Mantel-Haenszel risk ratios. For 12.5 mg versus placebo, the reported estimate is 1.188, with a 95% confidence interval from 0.911 to 1.548 and p = 0.202. For 25 mg versus placebo, the reported estimate is 1.348, with a 95% confidence interval from 1.045 to 1.739 and p = 0.021. These are the sponsor’s own analyses and should be treated as the primary inferential results reported in the registry.

The simple recalculations use the posted arm counts to estimate unadjusted risk differences. They produce 0.056 for 12.5 mg versus placebo and 0.103 for 25 mg versus placebo, with their own confidence intervals and p-values. Risk differences and risk ratios use different scales, and the unadjusted method is not the same as the sponsor’s Cochran-Mantel-Haenszel analysis. The recalculations are therefore not a replication of the sponsor’s result.

The registry record flags a discrepancy between reported and recalculated results. In keeping with that flag, the sponsor’s own analysis takes precedence. The recalculation can help readers understand the posted counts in a simple comparison, but it should not override the reported analysis or be presented as the trial’s official adjusted result.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists 11 outcome measures and 24 analyses. Multiple outcomes and comparisons raise a multiplicity question: if many hypotheses are tested, some may appear statistically notable by chance even when there is no corresponding underlying effect. Appropriate interpretation depends on whether the outcomes were prespecified, whether a hierarchy was used, and whether p-values or confidence intervals were adjusted for the number of analyses. Those details are not reported in the registry record.

The primary endpoint is identified, but the record does not state a complete outcome hierarchy or a multiplicity-control procedure. As a result, the sponsor-reported p-values can be described as reported, but the record does not establish whether they account for the full family of outcomes and comparisons. The secondary results warrant particular caution because they form a broad set of measures and analyses.

The stated primary analysis population is the ITT analysis set, including all randomized patients except patients found to have been randomized multiple times within the program at different centers. The registry does not explain how missing primary outcome data were handled, whether any imputation was used, or how incomplete follow-up was treated. Those matters are not reported in the registry record. Missing-data decisions can affect both the estimated treatment contrast and its uncertainty, so the posted population definition alone is not enough to assess their impact.

Further information about the statistical analysis plan, interim analyses, and original sample-size assumptions is not reported in the registry record. Without those details, readers cannot determine from the registry alone whether all planned analyses are represented or whether the reported analysis followed a prespecified plan. These are limitations of the available reporting, rather than evidence that a particular analysis choice was made.

16. 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 2% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: accidental overdose (0.9%), pancreatitis (0.4%), pneumonia (0.4%), sepsis (0.4%), brain contusion (0.4%).

The registry reports serious adverse events for each safety group using both the number at risk and the number affected. The posted figures are 14 of 230 for NKTR-118 12.5 mg, 8 of 232 for NKTR-118 25 mg, and 12 of 231 for placebo. These are serious adverse event counts as recorded in the registry. They should be read as descriptive summaries; they do not by themselves establish that one treatment caused more or fewer events than another.

The registry also lists the most frequent serious adverse event terms and their reported percentages: ACCIDENTAL OVERDOSE at 0.9%, and PANCREATITIS, PNEUMONIA, SEPSIS, BRAIN CONTUSION, and POST LAMINECTOMY SYNDROME each at 0.4%. The record does not provide enough context in these summaries to assess event timing, relatedness to study drug, or comparative uncertainty. Those details are not reported in the registry record.

Serious adverse events are distinct from the other adverse-event counts, which are reported separately. Death counts are not reported in the record’s posted safety summaries. These safety figures are not a complete assessment of risk, and they should not be used alone to make treatment decisions.

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

The registry results describe a randomized comparison of two NKTR-118 doses with placebo on a prespecified binary responder outcome. The posted counts were higher in both active-treatment arms than in the placebo arm. The sponsor’s reported analysis did not find a statistically notable difference for the 12.5 mg comparison under its stated method, while the 25 mg comparison had a reported risk ratio above 1 and a confidence interval above 1. These are descriptions of the posted analyses, not proof of a universal effect.

A statistically notable result does not establish that an effect is clinically important. The risk ratio communicates relative response, while the recalculated risk difference gives an unadjusted absolute comparison. Neither measure alone determines the importance of the endpoint to patients. The registry does not report a threshold for clinical importance or enough contextual information to judge that question.

The findings also do not answer every question about opioid-induced constipation. The primary endpoint reflects a particular responder definition over a specified period and does not summarize all symptoms, quality of life, long-term outcomes, or safety considerations. The secondary outcomes broaden the description but include multiple measures with analysis details that are not fully reported.

Confidence intervals and p-values address statistical uncertainty under their methods and assumptions. They do not remove uncertainty about missing data, multiplicity, model specifications, or the completeness of registry reporting. In particular, the registry record flags a discrepancy between the sponsor analysis and simple recalculations; the sponsor’s own analysis takes precedence.

The results do not establish what would happen in populations or settings not described in the registry, and they do not provide medical advice. They are best understood as the trial’s posted statistical evidence for its defined population, treatment arms, endpoint, and analysis methods.

18. Why This Trial Matters Statistically

This trial illustrates how a binary responder endpoint can make a clinical question easy to state while still requiring careful statistical interpretation. Patients are classified according to a threshold-based definition, and the resulting counts support comparisons of response probability. The threshold is clinically interpretable, but it also discards information about how far individual patients are from the response criterion.

It also shows why effect measures matter. A risk ratio expresses a relative comparison, while a risk difference expresses an absolute separation in response probability. The registry’s sponsor analysis reports risk ratios, whereas simple recalculations use risk differences. These results can help readers understand different aspects of the same posted arm summaries, but they are not equivalent analyses. The record’s discrepancy flag makes it especially important to distinguish the sponsor’s analysis from the recalculations.

The study also includes a broad set of secondary outcomes. This offers multiple perspectives on bowel-related outcomes, but creates a multiplicity concern when interpreting isolated p-values. Without a reported hierarchy or adjustment procedure, the evidential weight of secondary findings is limited.

Finally, the record demonstrates that precision and reporting detail are essential to interpreting an estimate. Confidence intervals show how much uncertainty surrounds the reported comparisons, while missing-data methods, model specifications, and original design assumptions are not fully available in the registry record. These limits shape what can be concluded from posted results, even when the trial design is randomized and blinded.

19. 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 does not report the original sample-size justification or the assumptions used to design the trial. The planning illustrations based on observed effects should not be confused with the study’s original power calculation. The randomization procedure, allocation stratification, and details of who was masked are also not reported in the registry record, beyond the stated randomized, double-blind, triple-masked, parallel design.

The record identifies the ITT analysis set and its exception for patients randomized multiple times at different centers, but does not describe how missing outcome data were handled. Further details about follow-up completeness, imputation, or sensitivity analyses are not reported. The sponsor’s primary method is named, but the strata and full statistical model details are not posted in the registry record.

The discrepancy between sponsor analyses and simple recalculations means that the recalculated results should not be substituted for the sponsor’s reported inference. The registry record does not explain the source of the discrepancy. The record also lists multiple outcomes and analyses without reporting a multiplicity procedure or complete hierarchy. These omissions limit interpretation of secondary findings and of isolated p-values.

The posted safety summaries provide event counts and selected serious adverse event terms, but do not provide the detail needed to assess timing, relatedness, or comparative precision. The registry does not report death counts in the posted safety summary. These limitations concern what can be learned from the registry record and do not, by themselves, indicate that the trial analyses were invalid.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Assessment of Efficacy and Safety in Patients With Non-cancer-related Pain and Opioid-induced Constipation — NCT01323790.
• Registry record last updated 2015-06-02; status last verified 2015-05.
• Results first posted 2015-06-02.
• 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.

23. Record Summary

NCT01323790 was a completed Phase 3 randomized, triple-masked, parallel-group, placebo-controlled study of oral NKTR-118 in patients with non-cancer-related pain and opioid-induced constipation. The primary outcome was responder status during Weeks 1 to 12, defined using spontaneous bowel-movement frequency, improvement over baseline, and response across the treatment weeks.

The sponsor reported a Cochran-Mantel-Haenszel risk ratio of 1.188 for NKTR-118 12.5 mg versus placebo and 1.348 for NKTR-118 25 mg versus placebo. The registry record flags a discrepancy with simple unadjusted recalculations, so the sponsor’s own analysis takes precedence. The record also includes secondary outcomes and serious adverse event summaries. Multiplicity procedures, missing-data handling, and original design assumptions are not reported in the registry record.