Evaluation of Utility of Ultrasound Guided iPACK Block for Knee Extension After Total Knee Arthroplasty.: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Evaluation of Utility of Ultrasound Guided iPACK Block for Knee Extension After Total Knee Arthroplasty. (NCT03353233), a randomized phase 4 study. The primary outcome is Number of Participants Able to Hyperextend the Knee After Surgery.

2. Clinical Question

This question focuses on an early measure of knee extension rather than a comprehensive measure of recovery. The registry also lists walking distance, pain, and cumulative opioid consumption as secondary outcomes, measured at their specified postoperative times. Those outcomes provide related but distinct information: they address mobility, reported pain, and medication consumption, rather than the primary count of participants able to hyperextend the knee.

3. Trial Design

The registry identifies this as a Phase 4, randomized, double-masked, parallel-group trial. Enrollment was 50, with 25 participants listed in the iPACK Block Group and 25 in the Sham Group. The record identifies Duke University as the sponsor and gives the study status as completed. The recorded study start was 2018-05-03, and the primary completion date was 2021-01-22.

Participants were assigned to a ropivacaine iPACK block or a saline sham. The sham is described as using the same nerve block technique with an inactive salt-water solution. Although the study is labeled double-masked, which parties were masked and how masking was maintained are not reported in the registry record. The method used to generate the random assignment and the procedures used to conceal allocation are also not reported in the registry record.

The primary outcome was a participant count for ability to hyperextend the knee within 8 hours. Three secondary outcomes are listed: distance walked on postoperative day 0, pain measured at 24 hours using a numerical rating scale, and cumulative opioid consumption at 24 hours. The registry lists 4 outcome measures overall, consistent with one primary outcome and three secondary outcomes.

Details needed to reconstruct the trial's full conduct and analysis are limited in the registry record. Eligibility criteria, participant flow, the analysis population, handling of missing outcome data, and the original sample-size justification are not reported in the registry record. The trial's own prespecified statistical methods and any interim analyses are also not reported in the registry record. The planning illustrations accompanying the results are based on observed effects and are not evidence of the trial's original design assumptions.

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

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 Participants Able to Hyperextend the Knee After Surgery, measured over Within 8 hours.

The primary endpoint is the number of participants able to hyperextend the knee after surgery, assessed within 8 hours. It is a binary outcome at the participant level: each participant either met the stated ability criterion or did not. The registry reports counts rather than a mean measurement, and gives 4 participants in the iPACK group and 3 in the sham group, with 25 participants listed in each group.

This endpoint was selected to address the study's stated interest in knee straightening shortly after surgery. A participant count provides a direct way to compare how often the defined outcome was observed in each group. It is not a measurement of the degree of extension, duration of the ability, or performance on a later assessment. Those details are not reported in the registry record.

The endpoint should therefore be interpreted as a specific early outcome, not as a complete summary of mobility, pain, physical therapy, or postoperative recovery. The registry lists walking distance, pain, and opioid consumption separately as secondary outcomes. Those measures complement the primary endpoint but do not change what the primary count represents. The posted result describes the observed counts and their uncertainty; it does not by itself establish the cause of any difference or settle questions about outcomes beyond the defined measure and assessment time.

7. Results Posted in the Registry

• iPACK Block Group: 16.0% (4/25) versus 12.0% (3/25) on control; risk difference 4.0 percentage points (95% CI -15.2 to 23.2), risk ratio 1.33 (0.33–5.36); unadjusted two-proportion z-test p = 0.684.

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.

Ambulation as Measured by Distance Walked After Surgery

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • iPACK Block Group: mean 120.36 versus 148.80 on control; difference -28.44 (95% CI -92.74 to 35.86), standardized effect d = -0.25; z-test p = 0.386.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between iPACK Block Group and the control. The interval gives the range of effects that remain compatible with the data.

Pain as Measure by Numerical Rating Scale (NRS) 11

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • iPACK Block Group: mean 4.64 versus 5.00 on control; difference -0.36 (95% CI -1.74 to 1.02), standardized effect d = -0.14; z-test p = 0.608.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between iPACK Block Group and the control. The interval gives the range of effects that remain compatible with the data.

Cumulative Opioid Consumption

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • iPACK Block Group: mean 47.52 versus 48.98 on control; difference -1.46 (95% CI -22.50 to 19.58), standardized effect d = -0.04; z-test p = 0.892.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between iPACK Block Group and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes cover three related but distinct postoperative domains: walking distance, pain, and cumulative opioid consumption. Together, they offer context for the primary measure of early knee hyperextension, but none is a substitute for that endpoint. Their different units and assessment times also mean that a coherent clinical interpretation cannot be obtained by treating them as a single combined measure.

Across the posted point estimates, walking distance is lower in the iPACK group, while the pain and opioid-consumption means are also lower in that group. The uncertainty intervals for the posted mean differences span both directions. This pattern does not provide a clear, consistent indication of a group separation across these outcomes, and it does not resolve the uncertainty in the primary result.

The comparisons are unadjusted. As a general statistical explanation, examining several outcomes creates multiple opportunities for an apparently notable result to arise by chance, especially if no adjustment or hierarchy among outcomes is specified. The registry record does not report a multiplicity strategy or a prespecified approach to interpreting the secondary outcomes. Their unadjusted results should consequently carry less weight than a prespecified primary analysis and should be treated as exploratory evidence rather than as independent confirmation.

The registry record lists no reported analyses for the secondary endpoints. The posted group summaries and comparisons can be described, but the record does not establish whether these were the analyses planned in advance, whether all intended measurements were available, or how missing observations were handled. The secondary outcomes are informative as descriptive context, but they do not provide a strong basis for claims beyond the specific measures and times recorded.

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

• Ambulation as Measured by Distance Walked After Surgery
• Pain as Measure by Numerical Rating Scale (NRS) 11
• Cumulative Opioid Consumption

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary because it records whether a participant was able to hyperextend the knee within 8 hours. For a binary outcome, a risk difference expresses the difference between the proportions experiencing the event in the two groups. The posted estimate is 0.04. Its 95% confidence interval runs from -0.152 to 0.232. Negative values indicate a lower event frequency in the iPACK group under the comparison's direction; positive values indicate a higher event frequency. The interval includes zero, the value representing no difference.

What does the confidence interval describe?

As a general statistical explanation, a confidence interval describes the uncertainty in an estimate under the method used to calculate it. It is not a range that guarantees the true value lies within its limits, and it is not a probability statement about the treatment effect. Here, the interval spans meaningful differences in both directions, so the point estimate alone should not be read as a precise estimate of the underlying contrast. The registry does not report the method used to construct the interval.

How should the p-value be read?

The posted unadjusted p-value for the primary comparison is 0.684. As a general statistical explanation, a p-value measures how unusual data at least as incompatible with a specified null hypothesis would be, if that hypothesis and the calculation's assumptions held. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of an effect. The registry record does not report the exact test used for this p-value, so no particular test procedure should be inferred.

How do the secondary outcomes differ?

The secondary endpoints are continuous measurements summarized by group means and standard deviations. Their comparisons use mean differences, where the sign depends on subtracting the sham-group mean from the iPACK-group mean. A mean difference describes a contrast in average values, not the distribution of individual outcomes. The standard deviation describes variation among participant measurements within a group; it is not the uncertainty of the group mean or the confidence interval for the difference. The posted continuous-outcome comparisons include confidence intervals and unadjusted p-values, but the registry does not report the statistical test procedures used to obtain them.

As a general statistical point, estimates and their intervals are more informative about magnitude and uncertainty than a significance label alone. For continuous outcomes, the interpretation also depends on the units and on what direction represents a more favorable value. For walking distance, pain score, and opioid consumption, those units and assessment times differ. A mean difference should therefore be interpreted within its own outcome definition and should not be compared numerically across these measures.

What does randomization contribute?

As a general statistical explanation, random assignment is intended to make treatment groups comparable on average with respect to both measured and unmeasured characteristics. In a small trial, chance imbalances can still occur. The registry identifies the study as randomized but does not report the randomization procedure, any stratification, or baseline characteristics. The results cannot therefore be assessed from the registry record for those details.

The parallel-group design means that the two groups received different assigned procedures during the study rather than crossing between them. Double masking is the registry's description, but the identity of the masked parties and the success of masking are not reported in the registry record. These design labels do not substitute for details about implementation.

Why can over-dispersion matter?

As a general statistical explanation, over-dispersion occurs when observed variability is greater than a statistical model assumes. If a model does not allow for that extra variability, its standard errors and intervals can be too small, making estimates appear more precise than warranted. The registry record does not report a model for the primary endpoint or a dispersion assessment. The primary result is presented as a count-based comparison, so there is no basis in the record to claim that over-dispersion was tested or adjusted for.

More generally, the registry record does not describe covariate adjustment, the intended analysis population, missing-data methods, or a protocol-defined approach to secondary outcomes. The comparisons should therefore be understood as the posted unadjusted summaries, not as evidence that particular modeling choices were prespecified. The posted information supports descriptive interpretation of group results and their reported uncertainty, while leaving important analytical details unreported.

11. Confidence Intervals and Precision

The primary risk difference is 0.04, and its 95% confidence interval extends from -0.152 to 0.232. The interval includes zero and includes negative as well as positive values. This means the posted data are compatible with a lower event frequency in the iPACK group, little or no difference, or a higher event frequency, within the limits represented by the interval. The estimate is therefore not precise enough to determine the direction of the underlying contrast with confidence.

Precision is distinct from whether a result crosses a conventional statistical threshold. The unadjusted p-value is 0.684, but the key interpretive point is that the interval is broad and spans both directions. A nonsignificant result does not establish equivalence. Equivalence would require a prespecified margin defining what differences are considered acceptably small, together with an analysis designed to assess that question; such a margin or analysis is not reported in the registry record.

The group counts are small, and the total enrollment was 50. With only 4 and 3 observed primary events, the estimate is sensitive to the limited amount of event information. The confidence interval communicates this uncertainty more directly than the point estimate alone. The registry record does not report additional primary analyses or sensitivity analyses that could show how the result changes under other assumptions.

As a general statistical explanation, a confidence interval concerns sampling uncertainty under the calculation used. It does not account automatically for every possible source of uncertainty, such as missing data, outcome measurement, or departures from the planned analysis. Relevant details about those issues are not reported in the registry record. The interval should be read as uncertainty around the posted comparison, not as a complete account of all uncertainty about the study.

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 primary-outcome planning figures are participants per arm, not a total for both groups. The planning illustration assumes a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. It uses the observed effect as a reference and considers detecting the stated fraction of that observed effect. The trial's own original sample-size justification and design assumptions are not reported in the registry record.

For planning at 100% of the observed effect, the illustration gives 1,181 participants per arm for 80% power and 1,580 participants per arm for 90% power. At 75% of the observed effect, it gives 2,036 participants per arm for 80% power and 2,725 participants per arm for 90% power. At 50% of the observed effect, it gives 4,438 participants per arm for 80% power and 5,940 participants per arm for 90% power.

As a general explanation, 80% power describes the probability of detecting an effect of the specified size under the planning assumptions if that effect is present; 90% power represents a higher probability under those same assumptions. Smaller effects are harder to distinguish from random variation and therefore require more participants. These are planning illustrations, not observed power.

The figures are calculated from the observed effect, which is itself uncertain, particularly given the small number of primary events. They should not be taken as proof that the observed effect is the true effect or as a recommendation about a future study. The record does not report the assumptions used to plan the original enrollment of 50.

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 = 0.120; treatment proportion p₁ = 0.160; average p̄ = 0.140.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.4907 = 0.9618.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4899 = 0.4123.
4. n = (0.9618 + 0.4123)² / (0.0400)² = 1,180.1, rounded up to 1,181 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 <- 0.12                          # control proportion
p1 <- 0.16                          # 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(3353233)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 1,181 (80% power), 1,580 (90% power)
 75% of observed effect: n per arm = 2,036 (80% power), 2,725 (90% power)
 50% of observed effect: n per arm = 4,438 (80% power), 5,940 (90% power)
power.prop.test: 1180.1 
Simulated power at n = 1,181 per arm: 0.796 (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. Multiplicity, Missing Data and Analysis Populations

The registry identifies one primary outcome and three secondary outcomes. It does not report a plan for controlling multiplicity, such as a prespecified hierarchy, adjustment across outcomes, or a rule for which comparisons would be considered confirmatory. When several outcomes are examined, the chance of at least one apparently unusual result can increase. As a general statistical explanation, multiplicity methods address that issue by changing how evidence is evaluated across a family of tests. Without a reported plan, the secondary comparisons should be read cautiously and as unadjusted.

The record lists no reported analyses for the secondary outcomes. It also does not report a detailed primary statistical analysis plan, the analysis populations, or whether the posted analyses follow a protocol-specified approach. The meaning of the unadjusted comparisons is therefore limited to the results as posted; the record does not establish whether covariates, subgroup analyses, or alternative models were considered.

Missing-data handling is not reported in the registry record. The group summaries list 25 participants in each arm, but that alone does not describe completeness for each endpoint, reasons for missing measurements, or how any missing observations were treated. Nor does it establish that every randomized participant contributed data to every analysis. Participant flow and analysis denominators for each outcome are not reported beyond the group summaries.

These omissions matter because missingness and analytical choices can affect estimates and uncertainty. As a general statistical point, analyses based only on observed outcomes may be biased if the availability of an outcome is related to its value or to group assignment. The registry record does not provide enough information to assess that possibility or to determine whether sensitivity analyses were conducted. No interim analysis plan is reported in the registry record.

15. 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.

The registry lists 25 participants at risk for serious adverse events in each group. It records 0 serious adverse events in the iPACK group and 0 in the sham group, along with 0 deaths in each group. The record also lists 25 participants at risk for other adverse events in each group and records 0 affected participants in both groups.

These figures describe what was recorded for the groups and categories in the registry. They do not show that no adverse event of any kind could have occurred, and they do not establish comparative safety with precision. With the listed group sizes, uncommon events may not be observed in a study even when they are possible. The registry record does not report detailed adverse-event definitions, collection procedures, severity information beyond the serious-event category, or follow-up duration for safety outcomes. The absence of recorded events should therefore be interpreted as a description of this trial's posted safety data, not as proof of no risk.

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

The posted primary result is a count comparison: 4 participants in the iPACK group and 3 in the sham group were able to hyperextend the knee within 8 hours. The estimated risk difference is 0.04, with a 95% confidence interval from -0.152 to 0.232 and an unadjusted p-value of 0.684. The estimate points toward a higher event frequency in the iPACK group, but the interval is compatible with differences in either direction and is not precise.

This result does not establish that the groups are equivalent, nor does it establish that the iPACK procedure produces a reliable difference in the primary outcome. It describes the outcomes observed in this randomized trial and the uncertainty in the posted comparison. The record does not report an equivalence or noninferiority framework, a clinically important difference threshold, or a detailed primary analysis plan.

The endpoint is limited to the ability to hyperextend the knee within 8 hours. It does not, on its own, describe the degree of extension, walking ability, pain, later recovery, or other aspects of function. The secondary outcomes address some related domains, but their unadjusted comparisons are also uncertain and do not settle the primary question.

The findings apply to the enrolled trial population and the procedures as recorded. Eligibility details, participant characteristics, missing-data methods, and analysis populations are not reported in the registry record, limiting assessment of how broadly the results may apply. The posted data should not be interpreted as medical advice or as a general conclusion about all uses of the block. They are a limited set of trial results with substantial uncertainty around the primary contrast.

17. Why This Trial Matters Statistically

This trial illustrates why an observed difference and a statistically persuasive estimate are not the same thing. The primary counts differ by one participant, and the estimated risk difference is 0.04. Yet its confidence interval, from -0.152 to 0.232, includes values on both sides of no difference. Reading the point estimate without its interval would understate the uncertainty.

It also shows why a nonsignificant comparison should not be equated with evidence of equivalence. The unadjusted p-value is 0.684, but the trial's limited event information leaves a broad range of plausible differences. A study can fail to show a clear difference without being able to rule out differences that may matter. An equivalence conclusion requires a defined margin and an appropriate analysis, neither of which is reported in the registry record.

The planning illustration highlights a related issue: sample-size calculations depend on the effect size chosen and on assumptions about the design and analysis. Smaller target effects require larger planned enrollment under the stated assumptions. Since these illustrations use the observed effect and the original design assumptions are not reported, they cannot be treated as a reconstruction of the trial's planning rationale.

Finally, multiple outcomes and incomplete reporting of analysis details complicate interpretation. The primary outcome has a clear stated time frame, while the secondary outcomes describe different aspects of postoperative experience. Without a reported multiplicity strategy, missing-data plan, or analysis population, readers should distinguish descriptive summaries from confirmatory evidence. These are broadly useful statistical distinctions when interpreting small randomized studies.

18. 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 result is based on a total enrollment of 50 participants, with 25 listed in each group, and only 4 and 3 observed primary events. The resulting confidence interval is broad and includes differences in both directions. This limits precision and makes the point estimate an uncertain guide to the underlying group contrast.

The registry record does not report eligibility criteria, participant characteristics, participant flow, or the analysis population. It is therefore not possible from the record to assess baseline comparability, determine how many participants contributed to each outcome, or judge the representativeness of the enrolled participants. Although randomization and double masking are recorded, their procedures and implementation details are not reported.

Several outcome and analysis details are also absent. The record does not report the primary statistical method, a multiplicity plan, missing-data handling, or interim analyses. No reported analyses are listed for the secondary outcomes. The secondary comparisons are unadjusted and cover several distinct measures, so they should be interpreted cautiously rather than as definitive corroboration of the primary result.

The primary endpoint is limited to ability to hyperextend the knee within 8 hours. The registry does not report additional detail about how that ability was assessed or whether the measure captures degree or duration of extension. Safety reporting is limited to the posted counts and does not include detailed definitions or collection methods. These registry-level limitations constrain assessment of both the results' robustness and their scope.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Evaluation of Utility of Ultrasound Guided iPACK Block for Knee Extension After Total Knee Arthroplasty. — NCT03353233.
• Registry record last updated 2021-12-21; status last verified 2021-11.
• Results first posted 2021-12-21.
• 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.

22. Record Summary

NCT03353233 is a completed Phase 4 randomized, double-masked, parallel-group trial sponsored by Duke University. It enrolled 50 participants, with 25 in the ropivacaine iPACK group and 25 in the saline sham group. The study start was 2018-05-03, and the primary completion date was 2021-01-22.

The primary outcome was the number of participants able to hyperextend the knee within 8 hours. The registry reports 4 participants in the iPACK group and 3 in the sham group; the risk difference is 0.04, with a 95% confidence interval from -0.152 to 0.232 and an unadjusted p-value of 0.684. Three secondary outcomes address walking distance, pain, and cumulative opioid consumption. The posted primary estimate is imprecise, and the registry record does not report important details of the original design assumptions, analysis plan, or missing-data handling.