Treatment With Iovera° for Total Knee Arthroplasty (TKA) Post-Operative Pain: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Treatment With Iovera° for Total Knee Arthroplasty (TKA) Post-Operative Pain (NCT03327220), a randomized na study. The primary outcome is Cumulative Opioid Consumption.

2. Clinical Question

The registry also describes questions about pain, knee-related outcomes, physical function, hospital services, and rehabilitation. Posted secondary outcomes cover change from baseline in KOOS JR, pain on the numeric rating scale, and Timed Get Up and Go tests. The primary endpoint is an opioid-use measure; it is not itself a direct measure of pain relief. The registry record does not report a prespecified definition of what would count as similar pain relief or how that condition would be assessed alongside the primary endpoint.

3. Trial Design

This was a prospective, randomized, controlled, parallel-group, post-market study of the iovera° device in people undergoing TKA. The record lists the study as completed, with enrollment of 124. Its listed start date is 2017-11-06 and its primary completion date is 2019-03-27. The phase is listed as NA. The sponsor is Pacira Pharmaceuticals, Inc.

The registry describes two groups: an iovera° device treatment group and a standard of care treatment group. The device group received presurgical cryoneurolysis 5 (+/- 2) days before surgery, in addition to standard surgical protocols. The standard care group received those protocols without the described device treatment. Allocation is listed as randomized, the model as parallel, and masking as none. The record does not report the method used to generate the randomization sequence or whether allocation was concealed.

The primary endpoint was assessed from the time of TKA surgery to 6 weeks after surgery. The study description says opioid consumption was converted to morphine milligram equivalents, verified by pill count at follow-up visits, and divided by the number of days to obtain TME. The registry describes the intent-to-treat population as all randomized participants, but defines the overall number analyzed as those with data available for analysis. The record does not report further details about how missing endpoint data were handled.

The posted results include a primary opioid-use outcome and secondary outcomes concerning KOOS JR, pain on the NRS, and TUG. Only three secondary outcomes are posted. The record does not report the original sample-size justification, a detailed statistical analysis plan, or whether interim analyses were planned or performed. These omissions limit what can be inferred about the rationale for the chosen enrollment or the intended analysis procedures.

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:

Analysis population for the primary outcome, as defined in the registry: Intent-to-treat (ITT) population included all participants who were randomized into the study. Overall number analyzed is the number of participants with data available for analysis.

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: Intent-to-Treat (ITT) population included all participants who were randomized into the study.

6. Primary Endpoint

The registry lists the primary outcome as Cumulative Opioid Consumption, measured over From the time of TKA surgery to 6 weeks post-TKA surgery.

The primary endpoint is cumulative opioid consumption over the period from TKA surgery through 6 weeks after surgery. The registry says opioid use was converted to morphine milligram equivalents, with participant consumption verified by pill count at follow-up visits. It then describes dividing cumulative morphine equivalent by the number of days to provide a total daily morphine equivalent, reported as TME. The endpoint therefore expresses opioid consumption as a daily-equivalent measure over the specified follow-up period.

Opioid consumption is relevant to the study question because the study was designed to investigate whether presurgical device treatment was associated with less opioid use after TKA while maintaining similar pain relief. However, opioid consumption is not a direct measure of pain. Its interpretation alongside pain outcomes matters, and the registry record does not report a formal criterion for determining whether pain relief was similar between groups.

For a continuous endpoint, a group mean describes the average observed value among participants with available data for that analysis. The reported standard errors describe the estimated precision of those group means; they do not describe the full spread of individual participant values. The posted primary values are 4.8 TME in the iovera° group and 6.1 TME in the standard care group. These are descriptive group averages, not by themselves evidence that the groups differ beyond chance variation. The estimated contrast and its uncertainty are needed to assess the comparison.

The endpoint is limited to the stated follow-up window. It does not describe opioid use outside that period or establish why participants used opioids. The registry record does not report additional details about the exact pill-count schedule or the handling of opioid use that could not be verified.

7. Results Posted in the Registry

• Iovera° Device Treatment Group: mean 4.80 versus 6.10 on control; difference -1.30 (95% CI -3.24 to 0.64), standardized effect d = -0.24; z-test p = 0.189.

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.

Area Under the Curve (AUC)/Time for Change From Baseline in Knee Injury and Osteoarthritis Outcomes Score (KOOS JR.) Overall Score Through 6 Weeks Post-TKA

• 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:
  • Iovera° Device Treatment Group: mean 10.30 versus 8.40 on control; difference 1.90 (95% CI -2.27 to 6.07), standardized effect d = 0.16; z-test p = 0.371.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Iovera° Device Treatment Group and the control. The interval gives the range of effects that remain compatible with the data.

AUC/Time for Change From Baseline in Timed Get Up and Go (TUG) Tests Through 6 Weeks Post-TKA

• 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:
  • Iovera° Device Treatment Group: mean -1.20 versus -0.40 on control; difference -0.80 (95% CI -4.02 to 2.42), standardized effect d = -0.09; z-test p = 0.626.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Iovera° Device Treatment Group and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes broaden the scope beyond opioid consumption to knee-related status, pain, and physical performance. Their overall pattern is not a single, uniformly precise signal across all measures. The estimates vary in direction and uncertainty, and the outcomes use different scales. The registry record does not provide enough information to reduce these distinct measures to one common interpretation or to claim that they consistently favor one group.

These outcomes relate to the primary result by addressing other parts of the study's stated question: whether the intervention was associated with changes in pain, function, and recovery alongside opioid use. They do not directly answer the primary opioid-consumption question. Nor does a secondary result, on its own, resolve the uncertainty in the primary comparison. The registry's stated aim of maintaining similar pain relief is especially difficult to evaluate from the primary endpoint alone, because opioid consumption and pain ratings are different measures.

Secondary findings generally carry less confirmatory weight when many outcomes are tested without a reported adjustment or prespecified hierarchy. The registry record lists five analyses overall, but does not report a multiplicity plan. Without such a plan, unadjusted secondary p-values can be more vulnerable to chance findings across multiple tests. This is a general statistical caution, not a claim that any particular posted result is false.

The KOOS JR sponsor analysis is labeled non-inferiority, but its margin is not reported in the registry record. A non-inferiority conclusion depends on that margin and on the analysis specification, so the label alone is insufficient to assess the claim. The posted secondary results are useful as descriptive and exploratory evidence, but their interpretation should remain tied to their endpoints, uncertainty, and incompletely reported analysis details.

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

• Area Under the Curve (AUC)/Time for Change From Baseline in Knee Injury and Osteoarthritis Outcomes Score (KOOS JR.) Overall Score Through 6 Weeks Post-TKA
• AUC/Time for Change From Baseline in Numeric Rating Scale (NRS) for Pain Through 6 Weeks Post-TKA
• AUC/Time for Change From Baseline in Timed Get Up and Go (TUG) Tests Through 6 Weeks Post-TKA

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is continuous, and the registry reports group means with standard errors. A mean is the arithmetic average of observed values in a group. A standard error describes the uncertainty in an estimated mean; it is not the same as the standard deviation, which describes the spread of individual observations. Keeping these measures distinct is important when reading the posted results: the primary outcome reports standard errors, whereas the TUG outcome reports standard deviations.

What does a mean difference represent?

A mean difference compares the average outcome in one group with the average in another. Its sign depends on the order of subtraction. The simple recalculation expresses the primary contrast as iovera° minus standard care, producing -1.3. The sponsor's reported difference is 1.3, which reflects the reverse ordering. The sign alone does not indicate benefit or harm; it must be read with the group labels, the definition of the outcome, and the direction of subtraction.

A mean difference is an estimate, not a certainty. Repeated samples from the same underlying populations could produce different estimates. A confidence interval gives a range of values compatible with the data under the analysis assumptions. If the interval crosses zero for a difference, it includes both a possible difference in one direction and a possible difference in the other. That does not prove there is no difference. It indicates that the observed data do not pin down the direction with high precision under that analysis.

What do the reported tests tell readers?

The sponsor reports one-sided t-tests for the posted analyses. A t-test compares group means while accounting for variability and sample size under its assumptions. A one-sided test evaluates evidence in a specified direction, unlike a two-sided test, which considers departures in either direction. The registry record does not report the full statistical analysis plan or the sponsor's prespecified direction and decision rules. The primary sponsor result is labeled superiority, and its reported confidence interval includes zero. Its p-value should be read as a test result under the stated one-sided method, not as the probability that the treatment has no effect.

The recalculated p-values are unadjusted, simple comparisons based on posted summary statistics. They are not a substitute for a prespecified sponsor analysis. In the primary outcome, the recalculated estimate and interval are also unadjusted. Since the discrepancy flag is false, there is no reported conflict requiring the sponsor analysis to take precedence over the recalculation under the reporting convention for this analysis.

Why do uncertainty and variability matter?

Results from a clinical study are subject to sampling variability: the participants observed are not every possible participant who could have entered the study. An estimate can therefore be compatible with a range of underlying group differences. Greater variability among participant outcomes generally makes a group mean less precise when other features are unchanged. The standard error reflects precision of the mean, while the standard deviation reflects variation among individual measurements. These concepts answer different questions and should not be interchanged.

Over-dispersion is a general statistical concern when observed variability is greater than a model assumes. A model that understates variability can make estimates look more precise than warranted. The posted continuous outcomes use mean comparisons, but the registry record does not report diagnostic checks or details that would establish whether a particular variance model or adjustment was used. No conclusion about such checks should be inferred from the summary results alone.

How should secondary analyses be treated?

The registry posts three secondary outcomes, and the record lists five analyses overall. Multiple comparisons raise a general concern: when many outcomes or tests are examined, the chance of finding a nominally unusual result somewhere can increase. Adjustments or a prespecified hierarchy can address this, but neither a multiplicity adjustment nor a testing hierarchy is reported in the registry record. The unadjusted secondary p-values therefore have less confirmatory weight than a single, clearly prespecified primary analysis.

The KOOS JR result is labeled non-inferiority in the sponsor analysis. Non-inferiority testing asks whether an outcome is not worse than a comparator by more than a prespecified margin. The margin is essential to the interpretation, and it is not reported in the registry record. The posted label and p-value cannot, on their own, show what margin was used or whether that margin was clinically justified. The recalculated unadjusted comparison answers a different, ordinary mean-difference question and should not be substituted for the sponsor's non-inferiority framework.

The TUG analysis is labeled superiority. Its sponsor-reported test and the simple recalculation are both comparisons of group means, but their p-values differ. Different analysis specifications, including one-sided versus two-sided testing and the handling of data, can produce different inferential results. The registry record does not give enough detail to identify every reason for that difference. Reporting both results with their methods makes the distinction visible rather than treating them as interchangeable.

In general, a p-value measures how unusual the data would be under a specified null model and test procedure. It is not a measure of effect size, clinical importance, or the probability that a hypothesis is true. An estimate and confidence interval provide complementary information about the direction and range of plausible values. For these results, uncertainty and incomplete reporting of analysis decisions are central to interpretation.

11. Confidence Intervals and Precision

The primary estimate is a mean difference of -1.3 in the simple unadjusted recalculation. Its confidence interval extends from -3.24 to 0.640. Because the interval includes zero, the data are compatible with no mean difference as well as with values on either side of zero under the recalculated analysis. The interval also spans estimates that differ substantially in direction and magnitude, so the primary contrast is not estimated with enough precision to establish a clear direction.

The sponsor reports the primary contrast in the opposite order, as 1.3, with a 95% confidence interval from -0.6 to 3.2. This interval also includes zero. It conveys the same broad point: the posted primary analysis does not precisely establish a nonzero difference. The sponsor's one-sided p-value is 0.084, while the unadjusted recalculated p-value is 0.189. These values come from different stated testing approaches and should not be treated as identical analyses.

A confidence interval is not a range guaranteed to contain the true effect, nor does it assign probabilities to individual values within the interval. In general, it is a range generated by a procedure that, across repeated studies under its assumptions, would cover the true value at the stated rate. Its practical value is that it displays uncertainty and the range of effect sizes not ruled out by the data and method.

The secondary estimates also have intervals that cross zero in their simple recalculations. Their widths reflect limited precision, and the measures use different units, so interval widths cannot be compared as though they represented the same outcome scale. For the KOOS JR analysis, interpretation of the sponsor's non-inferiority test additionally depends on a margin that is not reported in the registry record. Precision is therefore constrained not only by the intervals but also by missing details about the intended decision criteria.

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 sample-size figures are planning illustrations based on the observed effect, not the trial's original design calculation. For these continuous outcomes, the entries are participants per arm. The stated assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation; each calculation targets the stated fraction of the observed effect. The trial's own original sample-size assumptions are not reported in the registry record.

The 80% power column gives the estimated participants per arm for a future study to have an 80% chance of detecting the effect used in that planning row, if the assumptions hold and that effect is the true one. The 90% power column gives the corresponding planning figure for a 90% chance. Higher target power generally requires more participants under otherwise similar assumptions. For example, the primary-outcome row planning for 100% of the observed effect lists 271 participants per arm for 80% power and 363 participants per arm for 90% power.

Rows planning for 75% or 50% of the observed effect use smaller effects than the full observed effect. Smaller effects are harder to distinguish from random variation, so they require more participants per arm in these illustrations. The primary-outcome entries rise from 271 for the full observed effect to 482 for planning at 75% and 1,084 for planning at 50% in the 80% power column. These values are examples of the stated planning assumptions, not estimates of the enrollment needed under every possible design.

These figures are not observed power. They are prospective planning illustrations using the effect estimated in this study, and observed effects can be unstable. The sample-size curve should be read in the same way: as a representation of how required planning size changes as the effect targeted changes, not as a measure of what the completed trial achieved.

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, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = -1.300; pooled standard deviation σ = 5.400.
2. n = 2 × (1.96 + 0.842)² × 5.400² / -1.300² = 270.8, rounded up to 271 participants per arm for 80% power.

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

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
delta <- -1.3                      # observed difference in means
sigma <- 5.39973092080467                     # pooled standard deviation
n_per_arm <- function(power, frac = 1) {
  ceiling(round(2 * (z_a + qnorm(power))^2 * sigma^2 / (delta * frac)^2, 6))
}
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: n per arm = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(n_per_arm(0.80, f), big.mark = ","), format(n_per_arm(0.90, f), big.mark = ",")))

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

# Simulation: exact two-sample t-test using simulated means and variances
set.seed(3327220)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 271 (80% power), 363 (90% power)
 75% of observed effect: n per arm = 482 (80% power), 645 (90% power)
 50% of observed effect: n per arm = 1,084 (80% power), 1,451 (90% power)
power.t.test: 271.8 
Simulated power at n = 271 per arm: 0.802 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The sponsor's primary analysis is a one-sided t-test labeled superiority. It reports a difference in means of 1.3, a 95% confidence interval from -0.6 to 3.2, and p = 0.084. The estimate is reported in the reverse direction from the simple recalculation, which expresses iovera° minus standard care as -1.3. The group means themselves are 4.8 for iovera° and 6.1 for standard care. Reading the contrast direction alongside those means avoids interpreting a positive or negative sign without knowing the subtraction order.

The simple recalculation is an unadjusted comparison from the posted summary statistics. It gives a confidence interval from -3.24 to 0.640 and p = 0.189. Both analyses have intervals that include zero, though their reported methods and p-values differ. A one-sided sponsor test and an unadjusted recalculation should not be treated as the same procedure. The registry record does not report all details of the sponsor's analysis plan that could explain every difference between the calculations.

The discrepancy flag is false. Accordingly, the posted results do not identify a discrepancy for which the sponsor analysis would take precedence under the reporting convention. The sponsor's result remains the sponsor's own analysis, while the recalculation is a separate, simple comparison of posted summaries; readers should keep their methods and purposes distinct.

15. Multiplicity, Missing Data and Analysis Populations

The registry record lists a primary outcome and three posted secondary outcomes, and it reports five analyses overall. When several outcomes or tests are examined, the chance of at least one apparently notable result can increase even if there is no true difference on any outcome. This general issue is called multiplicity. Researchers may address it through adjustments, a testing hierarchy, or a prespecified distinction between confirmatory and exploratory analyses. The registry record does not report whether any such approach was used.

The primary endpoint is identified, which helps readers distinguish it from secondary measures. However, the registry does not report a complete statistical analysis plan, the intended hierarchy among analyses, or an adjustment for multiple testing. The secondary p-values are therefore best read as unadjusted results rather than as a set of fully controlled confirmatory tests. The record also does not report whether analyses beyond those posted were conducted.

The study description defines the intent-to-treat population as all participants randomized. It also says the overall number analyzed is the number with data available for analysis. The primary analysis lists 59.0 participants in the device arm and 60.0 in standard care; the analyzed counts differ by endpoint. The record does not explain the reasons for unavailable data, describe imputation, or state whether sensitivity analyses assessed the impact of missing outcomes. Thus, the extent to which missingness could affect the comparisons is not reported in the registry record.

Randomization supports a fair comparison when the randomized groups are analyzed in a way that preserves the assignment process, but missing data can complicate that interpretation. The registry's intent-to-treat definition does not by itself establish how missing outcomes were handled. The available record also does not report the method of sequence generation, allocation concealment, or interim analyses. These are reporting limitations; they should not be filled in by assumption.

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: bilateral pulmonary emboli (1.7%), r/o popliteal arterial aneurysm (1.7%), neuropsychotic/seizures (1.7%), anaphylaxis (1.7%).

The registry reports serious adverse events affecting 2 participants among 59 in the iovera° group and 2 among 60 in the standard care group. Other adverse events affected 4 among 59 in the device group and 3 among 60 in standard care. Deaths are reported as 0 in each group. These are descriptive counts in the registry record and do not by themselves establish whether an event was caused by the device, surgery, or another factor.

The listed serious event terms are Bilateral Pulmonary Emboli, R/O Popliteal Arterial Aneurysm, Neuropsychotic/seizures, and Anaphylaxis; each is listed as 1.7%. The registry's list does not specify the treatment group for each term or provide a complete event-level account in the information. The listed terms should therefore not be assigned to a particular group based on the group-level serious-event counts.

Adverse-event summaries are useful for describing what was reported during the study, but interpretation depends on event definitions, follow-up, attribution, and completeness of reporting. Further details about these aspects are not reported in the registry record. The counts should not be interpreted as a comparative safety rate or as evidence of causation.

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

The primary result describes average TME in the two randomized groups over the period from surgery through 6 weeks. The posted means are lower in the device group than in standard care, but the estimated contrast is uncertain: the sponsor's confidence interval includes zero, and the simple unadjusted recalculation also has an interval that includes zero. The record therefore does not establish a clear between-group difference in the primary outcome.

This result does not show that the groups are identical. An interval that includes zero can be compatible with no difference and with differences in either direction. The estimates also do not establish that the intervention does or does not reduce opioid use. They describe what was observed and the uncertainty that remains under the reported analyses.

The study's stated question also includes whether pain relief is maintained. Opioid consumption is not interchangeable with pain relief, and the primary result alone does not answer that part of the question. The registry posts secondary outcomes related to pain and function, but the results have their own uncertainty and analysis limitations. The record does not report a formal threshold for similar pain relief or the non-inferiority margin used in the KOOS JR analysis.

Nor do these data establish what would happen in settings or populations beyond the participants and protocols studied. The record describes presurgical device treatment 5 (+/- 2) days before TKA with standard care in both groups. It does not provide enough detail to evaluate all sources of missing data, analysis choices, or the clinical importance of the observed differences. The findings should be read as estimates from this completed study, not as medical advice or a universal conclusion about treatment.

18. Why This Trial Matters Statistically

This trial raises a useful statistical distinction between an observed difference and a precisely estimated difference. The posted group means differ, but the primary confidence interval includes zero and covers estimates in both directions. That pattern illustrates why comparing means alone is not enough: uncertainty around the contrast is essential to judging what the study can establish.

The study also illustrates that a primary outcome can be clinically relevant while still representing only one part of a broader question. Opioid consumption is the primary endpoint, whereas the stated study aim also concerns pain relief and other recovery measures. A numerical result on opioid use cannot automatically stand in for pain or function. Separate outcomes require their own definitions, estimates, and interpretation.

Its reporting highlights the importance of clear analysis specifications. The sponsor reports one-sided tests, including a non-inferiority analysis, while the posted summary allows simple unadjusted recalculations. Differences in test direction and framework matter. For non-inferiority, the margin is central, yet it is not reported in the registry record. For multiple secondary tests, the absence of a reported multiplicity approach makes nominal p-values less decisive.

Finally, outcome-specific analyzed counts and the absence of reported missing-data methods show why population definitions matter. A randomized design is a strength for comparison, but readers also need to know how randomized participants with unavailable outcomes were handled. These features do not erase the findings; they define the limits within which the estimates can be interpreted.

19. Limitations

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

The registry record does not report the original sample-size justification or the assumptions used to plan the trial. The planning illustrations based on observed effects are not a substitute for that information. Without the original rationale, readers cannot assess the study's intended ability to detect a prespecified clinically meaningful difference.

Further details of the randomization process are not reported, including sequence generation and allocation concealment. Masking is listed as none. The record does not describe whether outcome assessment or data analysis was masked, so no assumption should be made about those procedures.

The analyzed counts vary across outcomes, and the registry does not describe reasons for unavailable data, methods for handling missing values, or sensitivity analyses. The intent-to-treat population is defined as all randomized participants, but the endpoint-specific analyzed counts are based on participants with available data. This limits assessment of whether the posted estimates could be affected by missing outcomes.

The registry record does not report a multiplicity adjustment or a hierarchy for secondary analyses. It also does not report the margin for the KOOS JR non-inferiority analysis, which is necessary to assess that framework. Details of the full statistical analysis plan and interim analyses are not reported. In addition, the primary endpoint is an opioid-use measure, while the study aim includes similar pain relief; the record does not report a formal criterion linking those questions.

Finally, the available safety summary is aggregate. It reports affected-participant counts and selected serious event terms, but not the treatment group for each listed term or a detailed event-level description. These limitations concern what the registry record reports and do not demonstrate that unreported procedures or analyses were or were not conducted.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Treatment With Iovera° for Total Knee Arthroplasty (TKA) Post-Operative Pain — NCT03327220.
• Registry record last updated 2021-05-21; status last verified 2021-05.
• Results first posted 2021-05-21.
• 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.

23. Record Summary

NCT03327220 is a completed, prospective, randomized, controlled, unmasked, parallel-group post-market study of presurgical iovera° treatment in participants undergoing TKA. The device group received cryoneurolysis 5 (+/- 2) days before surgery in addition to standard care; the comparator group received standard care. Enrollment was 124.

The primary endpoint was TME from surgery through 6 weeks after surgery. The sponsor reported a one-sided superiority analysis with a difference in means of 1.3 and a 95% confidence interval from -0.6 to 3.2. A simple unadjusted recalculation expressed in the opposite direction gives a mean difference of -1.3, with an interval that also includes zero. The record additionally posts three secondary outcomes, but important details about multiplicity, missing data, and the non-inferiority margin are not reported.