Hydromorphone vs Fentanyl in Children Undergoing Tonsillectomy Surgery: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Hydromorphone vs Fentanyl in Children Undergoing Tonsillectomy Surgery (NCT04230681), a randomized early/phase 1 study. The primary outcome is Number of Patients Requiring Rescue Intravenous Opioid.

2. Clinical Question

This question concerns a defined postoperative event: whether a participant required additional intravenous opioid rescue during the stated observation period. It is distinct from a direct measure of pain intensity. The registry lists evaluation of participant pain as a secondary outcome, along with oxygen saturation and respiratory and postoperative nausea and vomiting events in the recovery unit and at home. Details of those secondary outcome results are not included in the posted comparison summarized by the primary outcome data.

The registry classifies the study as randomized, triple-masked, parallel, and early phase 1. These labels describe important aspects of the design, but the record does not say which people were masked, how masking was maintained, or how randomization was implemented. Those omissions limit what can be said about the procedures used to reduce bias.

3. Trial Design

The trial record describes a randomized, triple-masked, parallel study comparing hydromorphone with fentanyl in children undergoing tonsillectomy surgery. The brief summary also includes adenotonsillectomy. The study is classified as early phase 1 and its status is completed. Washington University School of Medicine is named as the sponsor.

The registry lists enrollment as 189. The primary outcome data list 90 participants in the hydromorphone arm and 90 in the fentanyl arm. The record does not explain the relationship between the enrollment figure and the outcome denominators, so these figures should be read as separately reported registry entries rather than reconciled into a single analysis population.

The recorded start date is 2020-02-26, and the primary completion date is 2022-04-01. The registry identifies the primary outcome as the number of patients requiring rescue intravenous opioid, measured up to 6 hours after surgery. It also lists four secondary outcomes: evaluation of participant pain, evaluation of participant oxygen saturation, respiratory and postoperative nausea and vomiting events in the recovery unit, and respiratory and postoperative nausea and vomiting events at home.

Randomization can help make treatment groups comparable on average, while masking can reduce some influences of treatment knowledge on care or assessment. These are general design principles, not confirmation of how they were achieved in this study. The registry does not report the randomization sequence, allocation concealment, the identities of masked groups, protocol deviations, or detailed arm procedures. The arm descriptions are blank, so treatment dosing and administration cannot be characterized from the record.

The record does not report the trial’s original sample-size justification, target enrollment rationale, or detailed statistical analysis plan. These missing details matter when judging how the posted analysis was selected and whether it followed a prespecified 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.

Overall Study

Reasons for not completing this period:

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 Number of Patients Requiring Rescue Intravenous Opioid, measured over up to 6 hours post surgery.

The primary endpoint counts participants who required rescue intravenous opioid up to 6 hours after surgery. It is a binary participant-level outcome: each participant either had the recorded event or did not. The registry reports the outcome as a number of participants, not as an average pain score or a count of opioid doses.

This endpoint is used to capture whether the initial postoperative analgesia was followed by a need for additional intravenous opioid rescue during the stated period. As a general statistical point, a binary endpoint can be summarized by the number of participants with the event and the number assessed in each group, then compared using measures such as a risk difference, risk ratio, or odds ratio. Each measure answers the same broad comparison in a different scale.

The endpoint does not by itself describe pain severity, the timing of rescue within the observation window, the amount of rescue medication, or events after the stated period. The registry lists pain evaluation separately as a secondary outcome, reinforcing that the primary endpoint and pain assessment are not interchangeable measures. The record does not report detailed criteria for deciding when rescue opioid was required or how endpoint data were collected.

The posted group counts are 48 participants with the event among 90 in the hydromorphone arm and 66 among 90 in the fentanyl arm. The interpretation depends on the recorded endpoint definition and the completeness and consistency of its assessment, details that are not reported in the registry record.

7. Results Posted in the Registry

• Fentanyl: 73.3% (66/90) versus 53.3% (48/90) on control; risk difference 20.0 percentage points (95% CI 6.2 to 33.8), risk ratio 1.38 (1.09–1.73); unadjusted two-proportion z-test p = 0.005.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary endpoint is binary at the participant level: requiring rescue intravenous opioid up to 6 hours after surgery is the event. The posted counts are 48 of 90 in the hydromorphone arm and 66 of 90 in the fentanyl arm. For binary outcomes, the basic group summaries are event counts and denominators. The resulting event proportions are the basis for the relative and absolute comparisons recorded for this outcome.

What does the risk difference describe?

The risk difference compares the event proportions by subtracting one group’s proportion from the other. In the posted comparison, the contrast is fentanyl versus hydromorphone and the risk difference is 0.2. A positive value means the recorded event proportion is higher in the fentanyl arm under that comparison’s direction. The risk difference is an absolute-scale measure: it describes the separation between proportions, rather than how many times one proportion is another.

As a general concept, absolute differences can be easier to relate to the observed event frequency than relative measures, but they depend on the outcome definition and the population being compared. Here the endpoint is rescue opioid requirement within a specified postoperative window. The record does not report additional clinical thresholds or a prespecified definition of a meaningful difference.

How do the risk ratio and odds ratio differ?

The reported risk ratio is 1.375, with interval endpoints 1.093 and 1.73. It compares event proportions as a ratio, with the fentanyl arm in the numerator for the posted contrast. A value greater than 1 indicates a higher recorded event proportion in that arm relative to the hydromorphone arm.

The reported odds ratio is 2.406, with interval endpoints 1.289 and 4.492. Odds are the chance of an event divided by the chance of no event; the odds ratio compares those odds between groups. As a general statistical point, an odds ratio and a risk ratio are not interchangeable. Their numerical values can differ, and an odds ratio should not be read as a direct ratio of event probabilities. The risk difference, risk ratio, and odds ratio therefore offer complementary but distinct descriptions of the same binary outcome.

What does the unadjusted p-value say?

The registry reports an unadjusted p-value of 0.005. In general, a p-value measures how unusual results at least as inconsistent with a null model as the observed result would be if that model and the test assumptions held. It is not the probability that the null model is correct, and it does not measure the size or clinical importance of a result. The registry does not report the test used, its assumptions, or whether any other inferential procedures were planned.

Unadjusted means the comparison is reported without a stated adjustment for other variables. Randomization can balance prognostic characteristics on average, but the record does not report baseline characteristics or an adjusted model. The posted estimate should thus be described as an unadjusted comparison rather than as an effect adjusted for participant characteristics.

Why does over-dispersion matter?

Over-dispersion is a general issue when observed variability is greater than a statistical model expects. It is especially relevant to count models, where an assumption about the variability of counts can affect standard errors and intervals. The primary outcome is reported as participants with a binary event, not as a recurrent-event count or a continuous measurement with a reported dispersion estimate. The registry does not report a model that would allow an assessment of over-dispersion. It would be inappropriate to infer that a particular over-dispersion correction was used.

What analysis details are unavailable?

The registry lists zero analyses and does not report a detailed statistical plan, analysis population, missing-data method, or covariate adjustment. It also does not state the interval confidence level. The sponsor’s analysis is not flagged as discrepant, but the absence of methodological detail still limits independent assessment of how the comparison was produced. The posted outcome counts and unadjusted comparison are the basis for interpretation; undisclosed model choices should not be assumed.

10. Confidence Intervals and Precision

The registry reports a risk difference of 0.2 for the fentanyl-versus-hydromorphone comparison. The interval endpoints are positive: 0.062 and 0.338. The reported risk ratio is 1.375, with endpoints 1.093 and 1.73, and the reported odds ratio is 2.406, with endpoints 1.289 and 4.492. The registry does not state the confidence level associated with these intervals, so that detail cannot be specified from the record.

In general, an interval estimate represents uncertainty around an estimated contrast under the method used to construct it. A narrower interval indicates greater precision on that scale, while a wider interval indicates more uncertainty. The interval is not a range that guarantees the true value falls inside it, and its interpretation depends on the statistical method and assumptions.

For the risk difference, the reported interval lies on the positive side of zero. For the relative measures, the reported intervals lie above the no-difference value of one. These are descriptions of interval placement, not proof that the result is free of bias or that its magnitude is important. Interval estimates account for sampling uncertainty under their construction; they do not automatically account for missing data, measurement error, protocol deviations, or unreported design features.

The event counts and denominators provide context for the amount of information in the comparison. The registry does not report subgroup intervals or adjusted estimates, so precision cannot be assessed for such analyses. The reported intervals should be interpreted as applying to the posted comparison and the stated primary endpoint, not to every secondary outcome or to a broader population without further evidence.

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 sample-size illustrations are planning calculations based on the observed effect, not descriptions of the trial’s original design. They give participants per arm for 80% power and participants per arm for 90% power. The assumptions 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 a stated fraction of the observed effect.

For planning at 100% of the observed effect, the illustration gives 90 participants per arm for 80% power and 120 participants per arm for 90% power. For planning at 75% of the observed effect, it gives 166 participants per arm for 80% power and 221 participants per arm for 90% power. For planning at 50% of the observed effect, it gives 381 participants per arm for 80% power and 509 participants per arm for 90% power.

In plain terms, the 80% power column describes a planning target intended to give the assumed design an 80% chance of detecting the chosen effect under the calculation’s assumptions. The 90% power column uses a higher target probability of detection. Smaller effects require more participants under these assumptions, which is why the illustrated per-arm requirements increase as the fraction of the observed effect decreases.

These figures are planning illustrations, not observed power. They do not establish the power the completed trial had, and they do not show that the trial was planned using these assumptions. The registry does not report the original sample-size justification or the trial’s original design assumptions.

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, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.533; treatment proportion p₁ = 0.733; average p̄ = 0.633.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6815 = 1.3357.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6667 = 0.5611.
4. n = (1.3357 + 0.5611)² / (0.2000)² = 89.9, rounded up to 90 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 <- 0.533333333333333                          # control proportion
p1 <- 0.733333333333333                          # 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(4230681)
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 = 90 (80% power), 120 (90% power)
 75% of observed effect: n per arm = 166 (80% power), 221 (90% power)
 50% of observed effect: n per arm = 381 (80% power), 509 (90% power)
power.prop.test: 89.9 
Simulated power at n = 90 per arm: 0.808 (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.

13. Multiplicity, Missing Data and Analysis Populations

The record lists a primary outcome and four secondary outcomes. It does not report a multiplicity plan describing whether or how inference across these outcomes was controlled. When several outcomes are tested, the chance of at least one apparently unusual result can increase; adjustment strategies and prespecification can affect interpretation. This is a general statistical concern, not evidence that the registry’s results were adjusted or unadjusted beyond the primary comparison explicitly marked unadjusted.

The record does not report a complete analysis plan, an outcome hierarchy beyond the primary and secondary labels, or whether any secondary outcomes were tested. It lists zero analyses. The posted primary comparison has an unadjusted p-value, but no multiplicity procedure is described. It would therefore be inappropriate to assume that secondary results were corrected, or to infer their statistical significance from the primary result.

Missing-data handling is also not reported. There is no account of the number randomized to each arm, participant flow, withdrawals, missing primary outcomes, or how incomplete observations were treated. The listed group denominators are 90 for each arm, while enrollment is listed as 189; the record does not explain how those entries relate. It is not possible to determine from these registry entries whether the endpoint counts represent all randomized participants, a particular analysis population, or a subset with available data.

The analysis population is not reported. The registry does not identify an intention-to-treat, per-protocol, or other population for the primary comparison. These labels have different implications: as a general principle, an intention-to-treat analysis follows assigned groups, while a per-protocol analysis applies specified adherence criteria. Neither approach should be attributed to this trial without a registry statement.

These omissions do not invalidate the posted counts, but they restrict assessment of robustness. Details about missingness, exclusions, multiplicity, and analysis populations would help readers understand which data contributed to each result and how uncertainty from analysis choices was handled.

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 0% reporting threshold.

Most frequent non-serious adverse event terms

The serious adverse event record reports zero participants with a serious event in the hydromorphone arm and zero in the fentanyl arm. Each arm lists 90 participants at risk for serious events. The death count is 0 in each arm. The registry’s serious-event term list is empty.

These figures describe the serious adverse event entries in the record. A zero count means no serious event was recorded in the listed group for this entry; it does not establish that the risk is absent. The registry does not report further detail about event definitions, collection procedures, follow-up completeness, or whether serious-event ascertainment covered a period beyond what is represented in the entry.

The record separately lists other adverse events affecting 15 participants in the hydromorphone arm and 12 in the fentanyl arm, with 90 participants at risk in each. These are not the serious-event counts. The registry does not provide event terms for these other adverse events in the registry entries, so their nature and severity cannot be characterized from these figures.

Adverse-event counts are descriptive and should be read alongside the recorded observation period and completeness of reporting. The available entries do not support a broader safety comparison beyond what is reported.

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

The posted primary outcome shows more participants recorded as requiring rescue intravenous opioid up to 6 hours after surgery in the fentanyl arm than in the hydromorphone arm: 66 of 90 compared with 48 of 90. The registry reports a risk difference of 0.2 for fentanyl versus hydromorphone, an unadjusted p-value of 0.005, and relative measures with reported intervals. These describe the registry’s primary comparison, not every aspect of postoperative pain or recovery.

The result does not by itself establish the cause of the observed difference. The study is randomized, which is an important design feature, but the record does not provide enough detail to assess implementation, masking roles, missing outcomes, or the analysis population. The comparison is unadjusted, and the method used to produce the inferential statistics is not reported. Statistical uncertainty intervals also do not account automatically for bias or unreported design issues.

The endpoint captures rescue intravenous opioid requirement during the period up to 6 hours after surgery. It does not state how intense pain was, how quickly rescue was needed, how much medication was used, or what happened after the specified period. Pain evaluation is listed as a secondary outcome, but results for it are not included in the posted primary comparison. The same is true of the listed oxygen saturation and respiratory and postoperative nausea and vomiting outcomes.

The safety entries report zero serious adverse events and zero deaths in each arm, alongside other adverse event counts. Those entries are limited by the detail available in the registry and should not be treated as proof of no risk. The record also does not explain the relationship between enrollment and the primary outcome denominators.

Accordingly, the strongest description is narrow: the registry reports different observed counts for the primary endpoint in the two arms, with an unadjusted comparison. Generalization beyond the trial’s recorded population, endpoint, and time window requires information not reported in the registry record.

16. Why This Trial Matters Statistically

This trial illustrates why the outcome scale matters in clinical biostatistics. The primary endpoint is binary and participant-based: whether rescue intravenous opioid was required within a defined period. The counts can be expressed as an absolute risk difference or as relative measures such as a risk ratio and odds ratio. Each provides a different perspective, and none should be mistaken for a direct measure of pain intensity.

It also shows why estimates and their uncertainty need to be read together. A point estimate describes the observed contrast, while an interval communicates uncertainty under the method used. The record reports intervals for the risk difference and relative measures, but does not state the confidence level or the procedure used to construct them. That missing information limits a fuller methods assessment.

Randomization, masking, and parallel allocation are meaningful design labels, but labels alone do not answer how the trial was conducted. Details about assignment, masked roles, analysis populations, missing data, and multiplicity help determine whether an observed contrast can be interpreted with confidence. Several of these details are not reported in the registry record.

The record also distinguishes completed study status from complete statistical reporting. It lists enrollment, arm denominators, endpoint counts, and a comparison, while leaving their relationship and several analytic choices unexplained. This is a useful reminder that registry results are not a substitute for a fully described protocol and analysis report.

Finally, sample-size illustrations based on an observed effect are not a retrospective measure of what the study was designed to detect. Their assumptions must be separated from the trial’s original planning, which is not reported. Clear distinctions among observed results, uncertainty, and hypothetical planning are central to responsible interpretation.

17. Limitations

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

The registry record leaves important trial details unspecified. The treatment arm descriptions are blank, so hydromorphone and fentanyl doses, routes, timing, and administration procedures are not reported. Although the trial is labeled triple-masked, the record does not identify which participants or study personnel were masked or explain how masking was maintained. The randomization procedure and allocation concealment are also not reported.

The outcome counts list 90 participants in each arm, while total enrollment is listed as 189. The registry does not explain the relation between these figures, provide participant flow, or state whether there were missing primary outcome observations. It also does not identify the population included in the comparison. This limits assessment of completeness and of how the posted result relates to all enrolled or randomized participants.

The statistical methods are incompletely described. The primary comparison is marked unadjusted and has an unadjusted p-value, but the test, model, interval method, and confidence level are not reported. There is no reported multiplicity plan, missing-data method, covariate adjustment, or detailed analysis plan. The registry lists zero analyses, making it difficult to assess what analyses were conducted beyond the posted comparison.

The endpoint is limited to rescue intravenous opioid requirement up to 6 hours after surgery. The record does not report results for the secondary outcomes listed, including pain evaluation, oxygen saturation, and respiratory and postoperative nausea and vomiting events. Details of endpoint adjudication and adverse-event follow-up are not reported either.

These limitations concern the detail available in the registry record. They do not change the recorded counts, but they constrain judgments about trial conduct, completeness, and the breadth of conclusions that can be drawn.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: Hydromorphone vs Fentanyl in Children Undergoing Tonsillectomy Surgery — NCT04230681.
• Registry record last updated 2024-12-18; status last verified 2024-11.
• Results first posted 2024-12-18.
• 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

The registry record describes a completed, randomized, triple-masked, parallel, early phase 1 trial of hydromorphone versus fentanyl in children undergoing tonsillectomy surgery. The brief summary includes tonsillectomy or adenotonsillectomy. Washington University School of Medicine is the named sponsor.

The primary endpoint is the number of participants requiring rescue intravenous opioid up to 6 hours after surgery. The posted counts are 48 of 90 in the hydromorphone arm and 66 of 90 in the fentanyl arm. The registry reports a risk difference of 0.2 and an unadjusted p-value of 0.005. Enrollment is listed as 189; the record does not explain how that figure relates to the primary outcome denominators.

The registry lists four secondary outcomes and safety entries, including zero serious adverse events and zero deaths in each arm. Details of the trial’s statistical plan, analysis population, missing-data handling, and original sample-size assumptions are not reported in the registry record.