Discontinuation vs Continuation of Long-term Opioid Therapy in Suboptimal and Optimal Responders With Chronic Pain: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Discontinuation vs Continuation of Long-term Opioid Therapy in Suboptimal and Optimal Responders With Chronic Pain (NCT02741076), a randomized phase 4 study. The primary outcome is Change in the Mean Average Pain Intensity (PI) Score on the 0-10 Numerical Ratings Scale (NRS).

2. Clinical Question

3. Trial Design

This was a Phase 4, randomized, parallel-group clinical trial described as double-blind, placebo-controlled, and triple-masked. The registry reports enrollment of 44 and lists four groups: structured discontinuation and continuation among suboptimal responders, and structured discontinuation and continuation among optimal responders. The posted arm sizes were 13 and 12 for the suboptimal-responder groups, and 3 and 4 for the optimal-responder groups. The trial status is terminated. Why it was terminated is not reported in the registry record.

The study compared structured discontinuation of long-term opioid therapy with continued opioid therapy for chronic low back pain. The medication options named in both interventions were morphine sulfate ER, oxycodone ER, and oxymorphone ER. The record does not describe the practical details of the discontinuation strategy or the rules used to determine which participants received each listed medicine. It also does not specify which individuals were masked, despite describing the trial as triple-masked.

The primary endpoint was change in mean average pain intensity, measured on a 0-10 Numerical Ratings Scale. Baseline was defined using available daily pain scores over a 7-day baseline period. The primary follow-up value was based on the 7 days preceding the Week 12 visit, with the timeframe stated as from baseline to the 1 week period prior to that visit. The registry gives the primary population as the Intent to Treat Population. It lists 13 outcome measures, while the posted record includes 12 secondary outcomes. No outcome analyses are listed in the registry record; the posted primary comparison is an available summary-statistic comparison for suboptimal responders.

The record identifies Member Companies of the Opioid PMR Consortium as sponsor. The study start and primary completion dates are recorded as 2016-09-14 and 2018-04-27. The registry does not report the reason for termination, the original sample-size justification, or a complete statistical analysis plan.

4. Participant Flow and Accounting

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

Before assignment: Prior to randomization, subjects gave consent and entered a pre-assignment period that assessed eligibility for the intervention phase of the study.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Intent to Treat Population

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 Change in the Mean Average Pain Intensity (PI) Score on the 0-10 Numerical Ratings Scale (NRS), measured over From baseline to the 1 week period prior to the Week 12 visit.

The primary endpoint measures change in mean average pain intensity from baseline to the period before the Week 12 visit. Pain intensity was assessed with the 0-10 Numerical Ratings Scale (NRS), where higher scores represent more pain and lower scores represent less pain. A change score describes movement from a participant’s baseline level rather than the follow-up level alone. A negative change therefore indicates a lower pain-intensity score relative to baseline, while a positive change indicates a higher score.

For baseline, the registry defines the score as the mean of available daily average pain-intensity scores during the 7-day baseline period. At scheduled post-randomization visits, the mean uses scores from the 7 days preceding the visit. The record says that if only one daily score is available, a mean is not calculated and the data point is considered missing. This rule makes the outcome dependent on having enough recorded daily scores to form the defined mean.

Change in pain intensity is relevant to the trial question because it places discontinuation and continuation groups on a common outcome scale and compares their changes over the specified period. It does not, on its own, describe every aspect of pain or functioning. The registry also lists outcomes related to sleep, depression, quality of life, and the number of suboptimal responders with pain improvement or worsening. The primary outcome is reported for the Intent to Treat Population, but the registry does not give further details about how missing daily ratings or missing follow-up values were handled in the analysis.

7. Results Posted in the Registry

• Continuation of Opioid Therapy Suboptimal Responder: mean -0.33 versus -0.22 on control; difference -0.11 (95% CI -0.84 to 0.61), standardized effect d = -0.12; z-test p = 0.761.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary outcome is a continuous measure: a numerical score that can take values across a scale. For each group, the registry reports a mean change and a standard deviation. The mean gives the average direction and size of change within the group. The standard deviation describes how dispersed individual observations are around that group mean. It is not the uncertainty of the mean itself, and it does not indicate that every participant experienced a change close to the average.

What does the group contrast represent?

The posted comparison for suboptimal responders is a mean difference of -0.113. It contrasts the average change in the structured-discontinuation group with the average change in the continuation group. Because the outcome is change from baseline, a negative change corresponds to a lower pain-intensity score than baseline. The contrast is a difference between group averages, not an individual-level change and not a percentage. The registry’s presentation identifies the continuation group as the comparison arm. The reported p-value is unadjusted, and the posted confidence interval is for this contrast.

Mean differences are useful because the NRS has the same units in both groups, so the contrast remains interpretable in scale points. However, statistical interpretation requires attention to both the estimated contrast and its uncertainty. A point estimate alone does not show how precisely the effect is estimated. The confidence interval extends across zero, and the p-value is 0.761; taken together, these summaries do not provide clear evidence of a group difference in this comparison.

Why does the standard deviation matter?

Variation among participants affects how precisely a group mean and between-group contrast can be estimated. When outcomes are more dispersed, the same number of observations generally yields less precise estimates than when outcomes are more tightly clustered. General statistical principle: standard deviations describe observed variability, while standard errors and confidence intervals describe uncertainty about estimated quantities. They answer different questions and should not be interchanged.

The suboptimal-responder arm standard deviations were 0.835 and 1.005. The optimal-responder arm standard deviations were 1.288 and 0.0. The last figure comes from an arm with 4 participants and should not be read as evidence that the outcome has no variability in the wider population. With a small group, a zero observed standard deviation only describes the values represented in that group; it does not establish that future observations would be identical.

What does the p-value tell the reader?

The unadjusted p-value of 0.761 is a measure of compatibility between the observed contrast and a null model of no group difference, under the assumptions of the test used. It is not the probability that the null model is true, the probability that the result is due to chance, or a measure of clinical importance. A large p-value does not prove that two approaches are equivalent. Equivalence requires an appropriate design and a prespecified margin, neither of which is reported in the registry record.

The word “unadjusted” matters because the registry lists multiple outcomes and responder subgroups. When many hypotheses are tested, the chance of at least one apparently notable result can increase. General statistical principle: methods such as a prespecified hierarchy or multiplicity adjustment can address some consequences of multiple testing. Whether any such strategy was planned or used is not reported in the registry record. The comparison should therefore be read as the posted unadjusted result rather than as a result known to account for every outcome or subgroup test.

What is the role of the confidence interval?

A confidence interval gives a range of values compatible with the data under the method’s assumptions, expressing uncertainty around the estimated contrast. It is not a range that contains a fixed proportion of individual participant outcomes. For this comparison, the interval includes zero, meaning the posted data are compatible with no difference as well as with contrasts on either side of zero. Its width is relevant: a wide interval indicates less precision than a narrow interval. The registry does not report confidence intervals for each arm mean or for the optimal-responder comparison.

General statistical principle: an interval’s interpretation depends on the analysis model and sampling assumptions. The record does not provide enough detail to evaluate all such assumptions or to determine whether covariate adjustment was planned. The posted contrast is presented as an unadjusted summary-statistic comparison, so it should not be mistaken for an adjusted estimate controlling for baseline characteristics.

How should the analysis population be understood?

The primary population is identified as the Intent to Treat Population. In general, an intention-to-treat analysis aims to retain participants in the groups to which they were assigned, regardless of later adherence or treatment changes. The phrase identifies the intended analysis population but does not specify how missing outcome values, withdrawals, or departures from assigned treatment were handled. The registry’s endpoint description explicitly treats some daily-score situations as missing, but the analysis method for those missing values is not reported in the registry record.

Overall, the statistics support a cautious descriptive reading: the posted suboptimal-responder group means changed in a negative direction, while the estimated contrast was -0.113 with an unadjusted p-value of 0.761 and an interval that includes zero. The available summary does not provide the detail needed to reconstruct a full statistical analysis or to make a definitive subgroup-wide claim.

10. Confidence Intervals and Precision

Precision concerns how narrowly the data locate the group contrast. The posted difference for suboptimal responders is -0.113, and its confidence interval extends from -0.841 to 0.615. Because this interval crosses zero, the results are compatible with no group difference as well as with differences in either direction. The interval’s width signals substantial uncertainty around the point estimate.

A confidence interval is not a prediction interval for individual participants and does not describe the range of changes experienced by most participants. It expresses uncertainty in the estimated group contrast under the analysis assumptions. The two endpoints should be read together with the point estimate: the estimate is near zero, but the interval permits a considerably broader range of contrasts than the point estimate alone suggests. The unadjusted p-value of 0.761 is consistent with the interval’s inclusion of zero, although the interval and p-value answer related but distinct inferential questions.

The arm sizes also affect how much confidence can be placed in subgroup summaries. The suboptimal-responder comparison has posted arm sizes of 13 and 12. The optimal-responder arms have 3 and 4, and the registry does not provide a confidence interval for an optimal-responder contrast. A mean from such a small group can be sensitive to individual observations, and the lack of a posted interval leaves its precision especially difficult to assess.

Precision should not be confused with importance. A narrow interval could estimate a small effect precisely, while a wide interval could leave both small and larger effects plausible. The registry does not report a threshold for a clinically important change, so the statistical summaries alone cannot determine whether any possible contrast would matter to patients. The observed comparison is also not a test of equivalence: the registry record does not report an equivalence margin or an analysis designed to establish equivalence.

11. 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 participants per arm for 80% power and participants per arm for 90% power. They are not total sample sizes or event counts. The calculations use a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each planning scenario uses a stated fraction of the observed effect: 100%, 75%, or 50%. These are planning illustrations based on the observed effect, not the trial’s original design justification.

The 80% power column indicates the number of participants per arm estimated to give an 80% chance of detecting the assumed effect under the stated planning assumptions, if that effect is truly present and the assumptions hold. The 90% power column gives the corresponding planning target for a 90% chance. Higher target power generally requires more participants for the same assumed effect. The figures are calculated for a two-arm comparison and should not be interpreted as enrollment targets for all four responder-by-treatment groups in this trial.

The rows for 100% of the observed effect call for 1,042 participants per arm for 80% power and 1,395 participants per arm for 90% power. Planning for 75% of the observed effect gives 1,852 participants per arm for 80% power and 2,480 participants per arm for 90% power. Planning for 50% of the observed effect gives 4,167 participants per arm for 80% power and 5,579 participants per arm for 90% power. Smaller effects need more participants because they are harder to distinguish from ordinary sampling variation.

These figures are not observed power. They are prospective illustrations that translate assumed effect sizes and planning choices into approximate sample sizes. They do not explain why the trial enrolled the number recorded or why it was terminated. The original sample-size assumptions and justification are not reported in the registry record. The planning calculation also reflects the observed effect used in its construction, so it should not be mistaken for independent confirmation of the trial result.

12. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

n is the number of participants in each arm, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = -0.113; pooled standard deviation σ = 0.921.
2. n = 2 × (1.96 + 0.842)² × 0.921² / -0.113² = 1,041.7, rounded up to 1,042 participants per arm for 80% power.

The smaller-effect rows in the table above repeat the same calculation with the effect multiplied by 0.75 and 0.5 (for ratios, applied to the logarithm of the ratio).

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
delta <- -0.113                      # observed difference in means
sigma <- 0.920512393672322                     # pooled standard deviation
n_per_arm <- function(power, frac = 1) {
  ceiling(round(2 * (z_a + qnorm(power))^2 * sigma^2 / (delta * frac)^2, 6))
}
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: n per arm = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(n_per_arm(0.80, f), big.mark = ","), format(n_per_arm(0.90, f), big.mark = ",")))

# Check against R's built-in function (t-based, so very slightly larger)
cat("power.t.test:", round(power.t.test(delta = delta, sd = sigma, power = 0.80)$n, 1), "\n")

# Simulation: exact two-sample t-test using simulated means and variances
set.seed(2741076)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 1,042 (80% power), 1,395 (90% power)
 75% of observed effect: n per arm = 1,852 (80% power), 2,480 (90% power)
 50% of observed effect: n per arm = 4,167 (80% power), 5,579 (90% power)
power.t.test: 1042.7 
Simulated power at n = 1,042 per arm: 0.798 (20000 replicates)

The simulation draws many sets of group means and variances at the planned sample size and counts how often the two-sample t-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

13. Multiplicity, Missing Data and Analysis Populations

The registry lists a primary outcome and multiple secondary outcomes, including pain-intensity change, improvement and worsening among suboptimal responders, sleep, depression, and quality of life. It also separates participants by responder status. Looking at several outcomes or subgroups creates a multiplicity issue: the more comparisons considered, the greater the chance that at least one result appears noteworthy by chance alone. This is a general statistical concern, not evidence that the trial’s analyses were invalid.

The posted p-value for the suboptimal-responder contrast is unadjusted. Whether the investigators used a testing hierarchy, adjusted for multiple comparisons, or designated which secondary outcomes were confirmatory is not reported in the registry record. The original statistical analysis plan is not reported, so the record does not establish which outcomes or subgroup contrasts were intended to support formal conclusions. No outcome analyses are listed in the registry record, and results for the listed secondary outcomes are not posted in the information used for this analysis.

The primary population is named as the Intent to Treat Population. The record does not describe the specific analysis set, participant flow, adherence handling, or whether any participants were excluded from the primary analysis. General statistical principle: intention-to-treat analysis seeks to preserve randomized group assignment, but the label alone does not explain how missing outcomes or protocol deviations were handled.

Missing data are especially relevant because the endpoint definition states that a mean is not calculated when only one daily pain score is available. The record does not report how many endpoint values were missing, whether missingness differed by group, or whether imputation, sensitivity analysis, or another method was used. These details matter because conclusions can depend on how incomplete observations are treated. The registry also does not report interim analyses, and no reason for trial termination is stated. These omissions make it difficult to assess the planned multiplicity strategy, completeness of outcome data, or the relationship between the posted results and the full analysis plan.

14. Safety Results

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

Deaths

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: urinary tract infection (7.7%).

The registry reports serious adverse events by arm. The structured-discontinuation suboptimal-responder group had 1 serious adverse event among 13 at risk; the continuation suboptimal-responder group had 0 among 12. The structured-discontinuation optimal-responder group had 0 among 3, and the continuation optimal-responder group had 0 among 4. The registry reports 0 deaths in each of the four groups.

These are event counts, not comparative risk estimates. The group sizes are small, particularly for optimal responders, and the counts alone do not establish whether an intervention caused an event or whether the groups differ in safety. The most frequently listed serious-event term was Urinary Tract Infection, recorded as 7.7%. The registry record does not give additional context for that term in the posted summary.

Other adverse events were reported in 9 of 13, 7 of 12, 2 of 3, and 1 of 4 participants across the four groups, respectively. These are the registry’s other-event counts and are separate from the serious-event counts. The figures should be interpreted as descriptive reporting over the recorded trial period, not as a complete comparison of safety or as proof that an event was caused by treatment. Further details about event definitions, timing, severity breakdowns, and attribution are not reported in the registry record.

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

The main posted comparison concerns suboptimal responders and measures change in average pain intensity from baseline to the period before the Week 12 visit. Both group means were negative, and the estimated between-group contrast was -0.113. The confidence interval includes zero, and the unadjusted p-value was 0.761. Together, these figures do not provide clear statistical evidence of a difference in mean change between the two groups in this comparison.

That conclusion is narrower than saying that the groups were identical. The confidence interval allows a range of effects, and the trial record does not report an equivalence design or margin. Nor does a non-significant result show that no individual experienced improvement or worsening. Group means summarize averages, while people’s experiences can vary. The registry does not post the primary comparison’s individual-level distribution or secondary improvement and worsening results.

The optimal-responder arm means are descriptive, based on 3 and 4 participants, and no formal contrast or confidence interval is posted for them. They cannot establish a separate treatment effect for that subgroup. More broadly, the registry does not report the original sample-size justification, full analysis plan, missing-data methods, or reason for termination. These gaps limit assessment of how the results relate to the trial’s intended analyses and how representative the posted summaries are of all randomized participants.

The findings therefore describe the available registry results rather than proving that either approach is better, worse, or equivalent. They do not support a treatment recommendation, and they should not be generalized beyond the trial population and outcome without further evidence. The registry’s safety counts likewise describe reported events; they do not establish causation or a definitive comparative safety profile.

16. Why This Trial Matters Statistically

This trial poses a statistically challenging question because it separates participants by response to long-term therapy and compares two strategies within those subgroups. Subgroup comparisons can be informative when planned and adequately supported, but they generally rely on fewer observations than an overall comparison. In this record, the optimal-responder groups are especially small, and no inferential contrast is posted for them. This makes the distinction between descriptive averages and evidence from a formal comparison essential.

The primary measure is a change score on a bounded 0-10 scale. Change scores make the comparison about movement relative to baseline, but interpretation still depends on variation, missing daily scores, and how the analysis handles the baseline and follow-up measurements. The registry defines the averaging windows and a rule for treating a day with only one recorded score as missing. It does not report the resulting amount of missingness or the analysis used to address it.

The suboptimal-responder contrast illustrates why a point estimate should not stand alone. The estimate of -0.113 is accompanied by an interval that crosses zero and an unadjusted p-value of 0.761. Those statistics communicate uncertainty, not proof of equivalence. The contrast is also only one among several listed outcomes and subgroup questions, while the multiplicity approach is not reported. Readers need both the estimate and the context of the analysis plan to judge how much weight to place on an individual result.

Finally, a terminated trial with a registry enrollment of 44 and no reported termination reason leaves questions about the study’s course and its intended precision unanswered. The planning illustrations show how assumed effect size influences sample-size requirements, but they are not evidence of the original design choices. These features make transparent reporting of subgroup methods, missing-data handling, and planned comparisons particularly important for interpreting the posted results.

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.

Several limitations are specific to the registry record. It marks the study as terminated but does not give the reason. It does not report the original sample-size justification, the stopping or termination process, or whether any interim analyses were conducted. Consequently, the reader cannot determine from the record whether the enrollment and duration reflect the original plan or a later change.

The primary comparison is posted only for suboptimal responders. Although mean changes are listed for optimal responders, their groups contain 3 and 4 participants, and no contrast or confidence interval is reported. The record also does not provide a formal interaction analysis to assess whether the treatment contrast differed by responder category. Any claim that responder status modifies the comparison would therefore go beyond the posted analyses.

Important analysis details are absent: the full statistical plan, the method used to calculate the contrast and confidence interval, any covariate adjustment, handling of missing outcomes, and the approach to multiple comparisons. The registry specifies that a daily mean is considered missing if only one daily score is available, but it does not report how such missing values were handled in the final analysis or how many values were missing. This prevents evaluation of potential bias from incomplete outcome data.

The brief arm descriptions are empty, and the registry does not describe the operational details of structured discontinuation. It also does not identify which parties were masked. The results are summary statistics rather than participant-level distributions, and the secondary outcomes are listed without posted analyses in this record. Finally, event counts are descriptive and lack additional context about event attribution and timing. These limitations constrain interpretation but do not by themselves show that the trial was conducted improperly.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: Discontinuation vs Continuation of Long-term Opioid Therapy in Suboptimal and Optimal Responders With Chronic Pain — NCT02741076.
• Registry record last updated 2019-11-06; status last verified 2019-10.
• Results first posted 2019-11-06.
• 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

NCT02741076 is a Phase 4 randomized, parallel-group trial comparing structured opioid discontinuation with continued opioid therapy among suboptimal and optimal responders receiving high-dose, long-term opioid analgesic therapy for chronic low back pain. It is described as double-blind, placebo-controlled, and triple-masked, and its status is terminated. The reason for termination is not reported in the registry record.

The primary endpoint was change in mean average pain intensity on a 0-10 Numerical Ratings Scale from baseline to the period before the Week 12 visit. For suboptimal responders, the posted mean difference was -0.113, with an unadjusted p-value of 0.761 and a confidence interval that includes zero. The registry lists outcome measures related to pain, sleep, depression, and quality of life, but does not post analyses for the secondary outcomes in this record.

The record does not report the original sample-size justification, complete statistical analysis plan, multiplicity strategy, or missing-data methods. The posted findings are best read as descriptive and uncertain rather than as proof of a difference or equivalence.