Safety and Efficacy Study of Hydromorphone Hydrochloride by Intrathecal Administration: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Safety and Efficacy Study of Hydromorphone Hydrochloride by Intrathecal Administration (NCT01709721), a randomized phase 3 study. The primary outcome is Proportion of Subjects Who Are Treatment Failures During the Double-blind Randomized Withdrawal Period.

2. Clinical Question

3. Trial Design

This was a phase 3, randomized, double-blind, parallel-group study with two arms. Its official title describes a controlled randomized withdrawal design evaluating hydromorphone hydrochloride delivered by intrathecal administration using a programmable implantable pump. The registry lists management of chronic pain as the condition and Piramal Critical Care, Ltd. as the sponsor. The study status is completed; the recorded start was 2013-02 and primary completion was 2018-02.

The randomized phase compared participants who remained on hydromorphone hydrochloride with participants whose hydromorphone was titrated downward. The control therefore represents withdrawal by dose reduction rather than absence of the drug. Both randomized groups are described as double-blind. The registry also describes an open-label dosing period before randomization: the primary endpoint's baseline pain was based on measurements from Days 77 to 83 while participants were on an optimal intrathecal hydromorphone dose. The randomized analysis period ran from Day 84 to the end of the study, with the primary outcome timeframe extending to the Day 119 visit.

Total enrollment was 153. The primary endpoint analysis population is specifically defined as randomized subjects in the intent-to-treat population; people who left during the open-label phase or did not qualify for randomization were not part of that endpoint analysis. The registry also reports an open-label-only, not-randomized group in its safety results. The randomization method, allocation concealment details, and the trial's original sample-size justification are not reported in the registry record. Although the registry names a programmable implantable pump as a device intervention, detailed device-management procedures 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.

Open Label Phase

Reasons for not completing this period:

Randomized Phase

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Intent-to-Treat - Randomized Subjects. Subjects in the Open Label Phase of the study who discontinued the study prior to the Randomization Phase and/or did not meet the criteria for randomization are not included in this analysis as they were not randomized to a treatment group.

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 Enrolled Subjects

6. Primary Endpoint

The registry lists the primary outcome as Proportion of Subjects Who Are Treatment Failures During the Double-blind Randomized Withdrawal Period, measured over 5 weeks [Baseline (Day 84) to Day 119 Visit].

The primary endpoint was the proportion of randomized subjects classified as treatment failures during the double-blind randomized withdrawal period. It covered five weeks, from baseline at Day 84 through the Day 119 visit. A participant met the definition after at least one of three types of event: an increase of at least 20 mm on VASPI versus baseline over five days; intolerable pain that, in the investigator's opinion, required intervention; or a pain-related intervention that violated the protocol between Day 84 and Day 119.

The registry defines randomized-phase baseline pain as the average of the last five days with daily pain measurements while the participant was on an optimal intrathecal hydromorphone dose, between Days 77 and 83 of the open-label dosing period. This gives the withdrawal-period measure a reference tied to the preceding treatment phase. A participant was not classified as a treatment failure for insufficient evaluable data, dropout for reasons outside the listed failure criteria, or withdrawal syndrome identified by COWS > 12 during the randomized phase.

A binary endpoint such as treatment failure records whether each participant did or did not meet the defined event criteria. It is used to summarize how often a clinically specified event occurred during a defined period, while combining the listed qualifying circumstances into one outcome. The registry does not report separate primary-outcome counts for each component, so the posted total cannot establish which component most often determined failure.

7. Results Posted in the Registry

• Hydromorphone Hydrochloride (Randomized/Double-Blind): 43.9% (18/41) versus 60.0% (24/40) on control; risk difference -16.1 percentage points (95% CI -37.6 to 5.4), risk ratio 0.73 (0.48–1.12); unadjusted two-proportion z-test p = 0.147.

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.

Brief Pain Inventory (BPI): Pain Severity, "Worst"

• 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:
  • Hydromorphone Hydrochloride (Randomized/Double-Blind): mean 5.62 versus 6.62 on control; difference -1.00 (95% CI -2.18 to 0.18), standardized effect d = -0.37; z-test p = 0.096.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Hydromorphone Hydrochloride (Randomized/Double-Blind) and the control. The interval gives the range of effects that remain compatible with the data.

Brief Pain Inventory (BPI): Pain Severity "Average"

• 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:
  • Hydromorphone Hydrochloride (Randomized/Double-Blind): mean 4.09 versus 4.78 on control; difference -0.69 (95% CI -1.65 to 0.27), standardized effect d = -0.31; z-test p = 0.157.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Hydromorphone Hydrochloride (Randomized/Double-Blind) and the control. The interval gives the range of effects that remain compatible with the data.

Brief Pain Inventory (BPI): Pain Severity Summary Measure

• 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:
  • Hydromorphone Hydrochloride (Randomized/Double-Blind): mean 4.19 versus 5.24 on control; difference -1.05 (95% CI -2.03 to -0.07), standardized effect d = -0.46; z-test p = 0.037.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Hydromorphone Hydrochloride (Randomized/Double-Blind) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The posted secondary outcomes cover several aspects of pain and its consequences, including pain severity, interference with function, a short-form pain questionnaire, rescue medication timing, patient global impression of change, and oral opioid supplement consumption. The registry lists nine posted secondary outcomes and reports analyses for some of them; not every listed outcome has a displayed result in the posted information. The results that are available do not all point with the same degree of statistical evidence, and they should be considered as a group rather than selected individually.

For the three pain-severity outcomes with values posted, the sponsor's ANCOVA analyses report p-values ranging from 0.016 to 0.164. The corresponding unadjusted recalculations are based on summary means and standard errors and are not the same as the ANCOVA analyses. These secondary findings add context to the primary treatment-failure comparison, but they do not replace it: pain scores are continuous measures, whereas the primary endpoint is a binary composite based on specified failure events.

Unadjusted secondary results carry less weight because several outcomes were assessed, and testing multiple outcomes creates more opportunities for a nominally notable result to arise by chance. Whether a multiplicity adjustment or prespecified hierarchy was used is not reported in the registry record. The posted secondary results should therefore be interpreted as supportive or exploratory context, not as independent confirmation of the primary endpoint. The full analysis plan, including how secondary hypotheses were prioritized, is not reported in the registry record.

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

• Brief Pain Inventory (BPI): Pain Severity, "Worst"
• Brief Pain Inventory (BPI): Pain Severity "Average"
• Brief Pain Inventory (BPI): Pain Severity Summary Measure
• Brief Pain Inventory: Interference With Function Summary Measure
• Short-Form McGill Pain Questionnaire (SF-MPQ): Summary Score
• Time to Rescue Medication After Randomization (Days)
• Patient Global Impression of Change (PGIC)
• Oral Opioid Supplement Consumption

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary: each randomized participant is classified as a treatment failure or not under the registry's definition. The reported group counts are 18 failures among 41 participants continuing hydromorphone and 24 among 40 participants assigned to downward titration. A risk difference expresses the contrast between the two groups' event proportions. The recalculated estimate is -0.161, with the comparison set up as hydromorphone minus control; a negative value indicates a lower observed event proportion in the hydromorphone group.

What does the confidence interval describe?

In general, a confidence interval describes the statistical uncertainty around an estimated effect under the assumptions of the method used. The primary recalculated 95% interval, -0.376 to 0.054, includes zero, the value corresponding to no risk difference. The data therefore do not pin down a single direction or magnitude with high precision. The confidence interval does not account automatically for every possible source of bias, such as limitations in outcome measurement or missing data; it quantifies uncertainty under the calculation's assumptions.

How should the p-value be read?

In general, a p-value measures how unusual data at least as incompatible with a specified null hypothesis would be if that hypothesis and the test assumptions held. The registry reports a chi-squared test for superiority with p = 0.147, and the unadjusted recalculation also gives p = 0.147. This result is not conventionally strong evidence against equal event proportions. It does not prove equality, and it does not tell how likely the observed effect is to be clinically important. The interval is important alongside the p-value because it displays a range of effect estimates consistent with the data and method.

Why can over-dispersion matter?

General statistical explanation: over-dispersion occurs when observed variability in count data is greater than a model's assumed variability. If a model ignores that extra variation, its uncertainty estimates can be too small and its tests too optimistic. The primary endpoint is a binary participant count, and the registry lists a chi-squared analysis; over-dispersion is not reported as an issue in the registry record. It should not be assumed to have affected this result.

What does randomization contribute?

In general, random assignment aims to make comparison groups similar on average with respect to both measured and unmeasured baseline factors. Double-blinding can reduce some differences in behavior or assessment related to knowledge of assignment. These design features support a group comparison, but they do not guarantee that every source of bias is absent, especially when follow-up or outcome data are incomplete. The exact randomization and masking procedures are not reported in the registry record, beyond the overall labels of randomized and double-blind.

The reported primary test is a chi-squared comparison of the randomized groups. A chi-squared test evaluates whether the observed distribution of outcome categories differs between groups, under the test's assumptions. The registry does not report a model-adjusted primary analysis, covariates, a missing-data sensitivity analysis, or a detailed statistical analysis plan. These aspects are not reported in the registry record.

For continuous secondary measures, the registry reports ANCOVA analyses. In general, analysis of covariance compares groups while accounting for covariates; the specific covariates and model specification are not reported in the registry record. The recalculated secondary mean differences are unadjusted comparisons derived from posted summaries, whereas the sponsor's ANCOVA p-values reflect a different analysis approach. A summary-based recalculation should not be mistaken for a reproduction of the sponsor's model.

Finally, a statistical test is only one part of interpretation. The endpoint definition, population, follow-up window, effect estimate, uncertainty, and reporting completeness all matter. A nominal p-value does not resolve the limitations of a composite endpoint or missing-outcome handling, and results across several endpoints raise the issue of multiplicity: the chance of chance findings can increase when many hypotheses are tested. Whether and how multiplicity was controlled is not reported in the registry record.

11. Confidence Intervals and Precision

The primary effect estimate is the unadjusted risk difference of -0.161, with a 95% confidence interval from -0.376 to 0.054. This interval crosses zero, meaning the posted data do not exclude no difference under this calculation. It also spans effects in both directions, so the point estimate alone would give an incomplete account of the uncertainty. The interval is a measure of statistical precision, not a guarantee that the true effect lies within those limits or that all possible study biases have been addressed.

The interval's width reflects the limited precision of a comparison based on 41 participants in one randomized group and 40 in the other, together with the observed event counts. A wider interval leaves greater uncertainty about the effect's magnitude. The registry's own primary analysis reports a p-value but not a sponsor-estimated effect interval, so the confidence limits are from the unadjusted recalculation rather than a registry-reported adjusted estimate.

General explanation: a confidence interval is most useful when read together with the point estimate and the outcome's meaning. It conveys which effect sizes are reasonably compatible with the data and calculation method, rather than dividing results into simply positive or negative. Because this interval includes effects on either side of zero, the primary result is inconclusive about the direction of the underlying difference. It should not be described as proof of equivalence or as proof that the groups had identical outcomes.

Precision is also outcome-specific. The interval for treatment failure does not automatically describe the precision of pain scores, safety events, or other secondary outcomes. The registry does not report confidence intervals for the sponsor's primary analysis, and its posted secondary analyses report p-values without sponsor confidence limits. Those missing estimates limit direct assessment of precision for the sponsor analyses.

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 illustrative calculations based on observed effects, not the trial's original design calculations. For the primary binary outcome, the figures are participants per arm. The same is true of the listed continuous secondary-outcome planning figures; there are no time-to-event planning figures in the posted calculations that would instead be expressed as total events.

The assumptions for these illustrations are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect. The trial's own original sample-size assumptions and justification are not reported in the registry record. These calculations are not observed power; they describe hypothetical planning under the stated assumptions.

The 80% power column means the approximate participants per arm needed, under those assumptions, to have an 80% chance of detecting the selected effect if that effect were the true one. The 90% power column represents a higher target chance of detecting that same selected effect, and therefore requires a larger planning sample. For the primary outcome, the illustration gives 151 participants per arm for 80% power and 201 for 90% power when planning for 100% of the observed effect. Planning for 75% gives 267 and 357 participants per arm, while planning for 50% gives 596 and 798.

Smaller target effects are harder to distinguish from random variation, so they require more participants under the same assumptions. The figures are not a retrospective judgment of whether the completed study was adequately powered, and they do not change the observed outcome or its uncertainty. They are best read as conditional planning examples, not as evidence that the trial's actual design used those targets.

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 = 0.600; treatment proportion p₁ = 0.439; average p̄ = 0.520.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7066 = 1.3848.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6973 = 0.5869.
4. n = (1.3848 + 0.5869)² / (-0.1610)² = 150.0, rounded up to 151 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 <- 0.6                          # control proportion
p1 <- 0.439024390243902                          # 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(1709721)
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 = 151 (80% power), 201 (90% power)
 75% of observed effect: n per arm = 267 (80% power), 357 (90% power)
 50% of observed effect: n per arm = 596 (80% power), 798 (90% power)
power.prop.test: 150 
Simulated power at n = 151 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

For the primary endpoint, the sponsor's reported analysis is a chi-squared superiority test with p = 0.147. The unadjusted recalculation from the posted group counts also gives p = 0.147. The record does not flag a discrepancy for the primary result, so the recalculation is consistent with the reported test at the displayed precision. The registry does not provide the sponsor's primary risk-difference estimate or confidence interval; the effect estimate and interval described in the interpretation and precision discussion are therefore unadjusted recalculations.

For secondary continuous outcomes, the sponsor reports ANCOVA p-values, while recalculated mean differences and their intervals are simple unadjusted comparisons from the posted summary statistics. These methods do not estimate uncertainty in exactly the same way: ANCOVA may account for covariates specified in the sponsor analysis, while the recalculation does not. The ANCOVA covariates and full model details are not reported in the registry record. The sponsor's own analysis takes precedence when a discrepancy is flagged; no such discrepancy is flagged in this record. Still, recalculated estimates should be read as descriptive checks, not replacements for the sponsor's analysis.

15. Multiplicity, Missing Data and Analysis Populations

The primary endpoint is defined for randomized subjects, and its analysis population excludes people who discontinued before randomization or did not meet randomization criteria. That definition is important: total enrollment of 153 is not the same as the population used for the primary comparison. The record identifies 41 participants in the continued-hydromorphone group and 40 in the downward-titration group for the primary outcome.

The endpoint definition also specifies how some incomplete or unusual outcomes were classified. A participant with insufficient data for evaluation, a dropout for a reason outside the listed failure criteria, or withdrawal syndrome identified by COWS > 12 was not classified as a treatment failure. The registry does not explain in detail how such cases were handled in the denominator, whether additional missing-data methods were used, or how sensitive the result is to alternative assumptions. Those details are not reported in the registry record.

Multiplicity arises when several outcomes or hypotheses are examined. Even if each test uses a conventional threshold, the chance of at least one apparently notable result can increase as the number of tests grows. This study includes a primary outcome and multiple secondary outcomes. The registry record does not report whether secondary analyses were adjusted for multiplicity, whether a hierarchy was specified, or which results were designated confirmatory. Accordingly, nominal secondary p-values should not be treated as if each were the sole prespecified test.

The complete statistical analysis plan, interim-analysis procedures, and sample-size justification are not reported in the registry record. The available information also does not state whether the primary analysis was adjusted for baseline values or other covariates. These omissions do not invalidate the posted results, but they limit evaluation of analysis choices, missingness, and the strength of claims across outcomes.

16. 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: drug withdrawal syndrome (5.0%), akathisia (2.5%), headache (2.5%), pneumonia (2.5%), cholecystitis (2.5%).

Safety results are reported for the randomized groups, the open-label-only group that was not randomized, and all subjects combined. Among the randomized groups, serious adverse events affected 2 of 41 participants continuing hydromorphone and 6 of 40 participants in the downward-titration control group. Other adverse events affected 35 of 41 and 36 of 40 participants, respectively. No deaths were recorded in either randomized group or in the larger safety groupings.

The registry lists Drug Withdrawal Syndrome at 5.0% among the top serious adverse-event terms, with Akathisia, Headache, Pneumonia, Cholecystitis, and Angina Unstable each listed at 2.5%. These are descriptive registry entries; the record does not establish from these figures whether an event was caused by an intervention. Serious-event counts are not the same as counts of all adverse events, and a participant may have more than one event. The safety figures for all subjects include people outside the randomized comparison, so they should not be interpreted as a randomized treatment contrast.

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

The posted primary results show fewer treatment failures in the group that continued hydromorphone than in the group whose dose was titrated downward, as reflected in the observed counts and negative recalculated risk difference. However, the unadjusted confidence interval includes no difference, and the reported primary p-value is 0.147. The results therefore do not establish a clear statistical separation between the randomized groups, while also not proving that their outcomes were identical.

The result applies to a particular comparison and period: randomized participants continuing intrathecal hydromorphone versus randomized participants undergoing downward titration, over five weeks from Day 84 to Day 119. It uses a composite definition that includes worsening pain, investigator-judged intolerable pain requiring intervention, or protocol-violating pain-related intervention. It is not a direct estimate of the effect of hydromorphone versus no treatment, nor does it describe every aspect of chronic pain management.

Precision matters. The interval allows a range of underlying group differences, and the posted primary analysis does not give a sponsor-estimated confidence interval. The secondary outcomes provide additional measures but are subject to separate analysis and multiplicity concerns. The safety counts are descriptive and include different analysis groups, so they cannot resolve efficacy questions or establish causation.

These findings should be understood as estimates from the registry's randomized withdrawal phase and its defined population. The registry record does not report full details of missing-data methods, covariate adjustment for the primary test, multiplicity control, or the original sample-size rationale. Those gaps limit how far the posted statistics can support broader conclusions.

18. Why This Trial Matters Statistically

This trial illustrates why a result should be read through its design, endpoint, population, and uncertainty rather than through a single p-value. The randomized withdrawal structure compares continuation with dose reduction after an open-label dosing period. That makes the control an active withdrawal strategy, not placebo, and the primary findings pertain to participants who entered the randomized phase.

The primary endpoint also combines several routes to treatment failure. Such a composite can capture more than one clinically relevant circumstance, but an overall count does not reveal which component drove the result. Component-specific primary counts are not reported in the registry record. The choice of the five-week randomized period and the baseline definition tied to recent open-label pain measurements are essential context for the estimate.

The primary effect estimate is accompanied by an interval that includes no difference, showing why uncertainty should be stated explicitly. The same principle applies to the secondary outcomes: multiple measures may add useful context, but unadjusted findings across many endpoints are not equivalent to one confirmatory result. Finally, registry-level reporting can leave important questions unanswered, including missing-data handling, multiplicity plans, and the sponsor's effect interval. Recognizing these limits is part of sound statistical interpretation, not a dismissal of the observations.

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 primary analysis is restricted to randomized participants, while the registry reports total enrollment of 153 and includes a separate open-label-only safety group. Outcomes among people who did not reach randomization are not represented in the primary comparison. The record does not give a detailed account of how selection into randomization may affect interpretation beyond the stated eligibility and population definitions.

The treatment-failure endpoint combines a pain-score increase, investigator judgment about intolerable pain, and protocol-violating pain-related intervention. These components may differ in how they are assessed, but the registry does not provide component-level primary counts. The endpoint also excludes specified cases from classification as treatment failures; detailed denominator and missing-data procedures are not reported in the registry record.

The primary reported analysis gives a chi-squared p-value but does not report a sponsor effect estimate or confidence interval. The interval discussed in the analysis is an unadjusted recalculation, not an adjusted sponsor estimate. Details of the randomization procedure, the primary model beyond the reported test, interim analyses, and the full statistical analysis plan are not reported in the registry record.

Several secondary outcomes are listed, and the available secondary analyses include ANCOVA p-values alongside unadjusted recalculations. Model covariates and multiplicity procedures are not reported in the registry record. These limitations mean that the secondary findings should be treated cautiously and that the posted summary does not answer every question about analysis choices or precision.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Safety and Efficacy Study of Hydromorphone Hydrochloride by Intrathecal Administration — NCT01709721.
• Registry record last updated 2021-11-04; status last verified 2021-10.
• Results first posted 2021-08-17.
• 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

The registry describes a completed phase 3, randomized, double-blind, parallel-group withdrawal study of intrathecal hydromorphone hydrochloride delivered using a programmable implantable pump for management of chronic pain. The primary endpoint was treatment failure during the five-week randomized period, comparing continued hydromorphone with downward titration.

There were 18 treatment failures among 41 participants continuing hydromorphone and 24 among 40 participants in the control group. The reported chi-squared p-value was 0.147. The unadjusted recalculated risk difference was -0.161, with a 95% confidence interval from -0.376 to 0.054. Secondary pain outcomes and safety events provide additional context, but their interpretation is limited by multiplicity and incomplete reporting of analysis details.