Study to Evaluate the Iovera° Device for Temporary Relief From Knee Pain: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study to Evaluate the Iovera° Device for Temporary Relief From Knee Pain (NCT02260921), a randomized na study. The primary outcome is Absolute Change From Baseline in Western Ontario and McMaster Universities Arthritis Index (WOMAC) Pain Subscale Score at Day 30.

2. Clinical Question

3. Trial Design

The registry describes a randomized, parallel-group, quadruple-masked study of the iovera° device for temporary relief of knee osteoarthritis pain. Its official title identifies it as prospective and multicenter. The comparator was a sham procedure using a similar device with no active therapeutic treatment. The registry lists Pacira Pharmaceuticals, Inc as the sponsor, records the status as completed, and gives an enrollment of 180. The start date is 2014-10-20 and the primary completion date is 2016-02. The phase is listed as NA.

The primary outcome was the absolute change from baseline in WOMAC pain subscale score at Day 30. The registry identifies an analysis of covariance, or ANCOVA, and reports least-squares means. The primary analysis population was per protocol rather than all enrolled participants: the registry definition requires randomization, delivery of the assigned treatment as intended by the device, and compliance with wash-out of pain medication before the baseline visit. The numbers analyzed in the posted primary outcome are 112 for iovera° and 56 for sham. These outcome-analysis counts should not be treated as a restatement of the enrollment figure.

The registry also lists secondary outcomes involving VAS and WOMAC scores and responder rates at Day 30 and Day 60. The primary outcome concerns the WOMAC pain subscale, whereas the secondary outcomes extend the assessment to other pain and symptom measures and to a later follow-up point. Details such as the full randomization procedure, the specific masking roles, and any procedures used to preserve masking are not reported in the registry record. The trial’s original sample-size assumptions and any planned interim analyses are also not reported in the registry record.

4. Participant Flow and Accounting

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

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Per-protocol Analysis Population included all participants who were randomized and underwent the assigned treatment where the treatment was successfully delivered as intended by the device and who are compliant with wash-out of pain medication prior to Baseline visit prior to study visit analyzed.

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) Analysis Population include all randomized participants who underwent the assigned treatment.

6. Primary Endpoint

The registry lists the primary outcome as Absolute Change From Baseline in Western Ontario and McMaster Universities Arthritis Index (WOMAC) Pain Subscale Score at Day 30, measured over Baseline to Day 30.

The primary endpoint is the absolute change from baseline to Day 30 in the WOMAC pain subscale. WOMAC is a disease-specific, patient-reported measure with questions about pain, stiffness, and physical function. The pain subscale consists of five questions, each scored from 0, meaning no pain, to 10, meaning extreme pain; the possible pain subscale score ranges from 0 to 50. Higher scores indicate worse pain, and the registry states that a negative change from baseline indicates improvement.

A patient-reported outcome is useful for evaluating pain because it directly records the participant’s experience rather than relying only on an external assessment. The WOMAC instrument also places the pain questions within a broader measure of osteoarthritis symptoms and function. This trial’s primary endpoint, however, is specifically the pain subscale, not the total WOMAC score or the stiffness and function subscales.

The endpoint compares the groups’ average changes, estimated as least-squares means in the registry’s ANCOVA analysis. The comparison is therefore about the relative change in reported pain over the baseline-to-Day 30 interval. It does not by itself describe every participant’s response, establish how long any change lasted beyond the measured period, or answer questions about outcomes not assessed by this endpoint.

7. Results Posted in the Registry

• Iovera° Treatment: mean -16.33 versus -8.79 on control; difference -7.54 (95% CI -11.45 to -3.63), standardized effect d = -0.62; z-test p = <0.001.

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.

Change From Baseline in Visual Analog Scale (VAS) at Day 30

• 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° Treatment: mean -39.20 versus -25.70 on control; difference -13.50 (95% CI -22.83 to -4.17), standardized effect d = -0.46; z-test p = 0.005.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Iovera° Treatment than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Change From Baseline in Total WOMAC Score at Day 30

• 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° Treatment: mean -77.18 versus -43.77 on control; difference -33.41 (95% CI -51.68 to -15.14), standardized effect d = -0.59; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Iovera° Treatment than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Change From Baseline in VAS at Day 60

• 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° Treatment: mean -37.46 versus -28.82 on control; difference -8.64 (95% CI -18.16 to 0.88), standardized effect d = -0.29; z-test p = 0.075.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Iovera° Treatment and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists secondary measures that broaden the outcome assessment beyond the primary Day 30 WOMAC pain subscale. They include VAS changes, total WOMAC changes, and responder-rate outcomes at Day 30 and Day 60. The posted continuous results generally show reductions from baseline in both groups, with larger estimated reductions in the iovera° group for the Day 30 measures and the Day 60 total WOMAC measure. The Day 60 VAS comparison is less clear in the unadjusted calculation, whose confidence interval includes zero.

This pattern is directionally compatible with the primary result for several measures, but secondary endpoints do not independently establish the primary finding. They may capture related aspects of pain and osteoarthritis symptoms, and they are measured at different times or using different scoring approaches. Agreement across related outcomes can add context, while a less conclusive comparison can reflect uncertainty rather than proving an absence of a difference.

Unadjusted secondary results carry less weight for several reasons. The registry does not report sponsor model-based analyses for the posted secondary comparisons in the available continuous outcome entries, so the simple calculations should not be mistaken for the trial’s full analysis plan. Also, assessing multiple outcomes increases the chance that some results will appear notable by chance. A multiplicity adjustment or a clear testing hierarchy can help control that issue, but such procedures are not reported in the registry record. The secondary findings are therefore best treated as supportive or exploratory context, not as a collection of separate definitive conclusions.

The endpoint list includes responder rates as well as continuous measures, but the posted numerical summaries described in the record do not permit a complete interpretation of every secondary endpoint. No additional values or conclusions should be inferred for endpoints without reported results. Overall, the secondary outcomes provide a broader but more qualified view of the trial than the primary Day 30 comparison alone.

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

• Change From Baseline in Visual Analog Scale (VAS) at Day 30
• Change From Baseline in Total WOMAC Score at Day 30
• Change From Baseline in VAS at Day 60
• WOMAC Pain Score Responder Rate at Day 30
• VAS Responder Rate at Day 30
• Change From Baseline in Total WOMAC Score at Day 60
• VAS Responder Rate at Day 60
• WOMAC Pain Score Responder Rate at Day 60

9. Statistical Interpretation

10. Statistical Methods Explained

What does ANCOVA contribute?

The registry identifies ANCOVA as the method for the primary analysis. In general, analysis of covariance compares groups while accounting for one or more covariates. When a baseline value is included, this approach can estimate a treatment-group contrast while taking account of baseline outcome levels. The registry record does not specify which covariates were included, how they were selected, or the model’s detailed assumptions. Those details should not be inferred from the name ANCOVA alone.

The reported quantities are least-squares means and a difference in least-squares means. In general, least-squares means are model-based group estimates, rather than necessarily being simple arithmetic averages of the observed participant values. The registry’s arm-level change estimates are -16.33 for iovera° and -8.79 for sham; its reported ANCOVA contrast is -7.53. The sponsor’s adjusted model estimate is the relevant posted inferential result. A separate simple recalculation from summary statistics is not a replacement for that model.

What does the endpoint’s sign mean?

The primary outcome is a continuous score, not a binary event count. Its direction is defined in the registry: a negative change from baseline indicates improvement. Accordingly, a negative between-group contrast means the estimated change is more negative in the iovera° group than in the sham group. This is a statement about the direction of the score difference, not a claim that every individual experienced improvement. General interpretation of continuous outcomes should consider both the estimated group contrast and its uncertainty, as well as whether the scale’s change is important to patients. A threshold for clinical importance is not reported in the registry record.

How should the p-value be understood?

In general, a p-value describes how compatible data are with a specified null model, under the assumptions of the analysis. It is not the probability that the null hypothesis is true, and it does not measure the size or importance of an effect. The registry reports p < 0.001 for the primary ANCOVA comparison. The record does not provide a detailed account of the p-value calculation or the complete model specification. The posted estimate and confidence interval are therefore important alongside the p-value: they describe the direction and range of values compatible with the reported analysis more directly than a threshold judgment alone.

What is the recalculated comparison?

The simple recalculation uses the posted arm-level means and standard errors to construct an unadjusted comparison. It is not the same as the sponsor’s ANCOVA, which estimates an adjusted difference in least-squares means. In the recalculation, the estimated difference is -7.54, with a confidence interval from -11.45 to -3.63 and p < 0.001. The pooled standard deviation used for the planning illustration is approximate, as indicated in the posted calculations. Such a summary-statistic reconstruction cannot reproduce covariate adjustment or other details of the sponsor’s model that are not present in the arm-level summaries.

Agreement in direction and close numerical alignment between an unadjusted reconstruction and an adjusted model can be reassuring as a check on the broad reading of the result, but the analyses answer slightly different statistical questions. The sponsor’s ANCOVA is the analysis reported by the registry for the primary outcome. The recalculation is best viewed as a transparent, simplified check rather than an alternative official result.

Why can over-dispersion matter?

General statistical explanation: over-dispersion occurs when variation in observed data is greater than a model assumes. It can make standard errors too small if the analysis does not account for the extra variability, which in turn can make confidence intervals too narrow and p-values too small. The primary outcome is continuous, and the registry reports standard errors for the arm estimates. It does not report an over-dispersion assessment, nor is an over-dispersion adjustment described. The concept is relevant to statistical modeling generally, but the record does not establish that over-dispersion was present in this trial.

The analysis population is another methodological consideration. The registry’s primary population excludes randomized participants who did not receive treatment as intended or did not meet the stated wash-out requirement. A per-protocol analysis can describe results among participants meeting those criteria, but it does not automatically answer the same question as an analysis retaining all randomized participants according to assignment. The registry record does not report a separate intention-to-treat primary result or enough detail to determine how deviations and missing outcome data were handled.

11. Confidence Intervals and Precision

The sponsor-reported primary comparison is -7.53 WOMAC pain points, with a 95% confidence interval from -11.48 to -3.58. A confidence interval is a range of values compatible with the data and the analysis under the method’s assumptions. In general, narrower intervals indicate greater precision and wider intervals indicate more uncertainty. The interval’s negative values are consistent with a greater average reduction in pain score for the iovera° group than for the sham group, given the registry’s direction convention.

The interval describes uncertainty about the estimated group difference; it does not describe the range of individual participant changes. It also does not account for limitations that are not represented in the model, such as unreported missing-data procedures or uncertainty about whether the endpoint captures outcomes beyond Day 30. Statistical precision and clinical importance are distinct questions. The registry record does not report a threshold for a clinically meaningful difference, so the interval alone cannot settle that question.

The simple recalculation gives a confidence interval from -11.45 to -3.63. That interval is close to the sponsor’s interval, but it comes from a different, unadjusted summary-statistic approach. The sponsor’s ANCOVA interval is the registry-reported inferential result. Differences between the two intervals should not be treated as a discrepancy in the registry’s result; the posted record marks no discrepancy.

For the Day 60 VAS secondary comparison, the recalculated interval extends from -18.16 to 0.882 and includes zero. This indicates greater uncertainty about the direction of that particular estimated difference than the primary interval conveys for the Day 30 WOMAC pain endpoint. It should be interpreted in the context of its secondary status and the fact that multiple outcomes were assessed. Confidence intervals provide a scale for uncertainty, not a verdict about the complete evidence or about effects outside the measured outcomes and time points.

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 assumptions. For these continuous outcomes, the figures are participants per arm, not total events. The planning method uses a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation; the effect to detect is the stated fraction of the observed effect. The registry’s original sample-size justification and assumptions are not reported in the registry record.

The 80% power column gives the planned participants per arm under the illustration’s assumptions for an 80% chance of detecting the selected effect if that effect were present. The 90% power column gives the corresponding number per arm for a 90% chance under those assumptions. These are planning concepts: power is calculated before observing trial results and depends on the chosen effect size, variability, significance level, and design assumptions. The listed values should not be interpreted as a measure of the chance that the trial result is true.

For the primary endpoint, planning for 100% of the observed effect gives 41 participants per arm for 80% power and 55 participants per arm for 90% power. Planning for 75% of the observed effect gives 73 and 98 participants per arm, respectively. Planning for 50% of the observed effect gives 164 and 220 participants per arm, respectively. The table and curve present how the illustration changes as the targeted effect becomes smaller. Smaller effects are harder to distinguish from random variation, so detecting them generally requires more participants.

These figures are not observed power. They do not describe the trial’s actual probability of success after its results are known, and they do not establish whether the original design was adequate. They are conditional planning examples built from the observed effect and the stated illustration assumptions. For other non-time-to-event outcomes, the same convention applies: the figures are participants per arm. The general note about total events applies to time-to-event tables, not to these continuous outcomes.

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 = -7.540; pooled standard deviation σ = 12.180.
2. n = 2 × (1.96 + 0.842)² × 12.180² / -7.540² = 41.0, rounded up to 41 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 <- -7.54                      # observed difference in means
sigma <- 12.1795236023714                     # 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(2260921)
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 = 41 (80% power), 55 (90% power)
 75% of observed effect: n per arm = 73 (80% power), 98 (90% power)
 50% of observed effect: n per arm = 164 (80% power), 220 (90% power)
power.t.test: 41.9 
Simulated power at n = 41 per arm: 0.792 (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 registry reports the sponsor’s primary analysis as an ANCOVA comparison of least-squares means. It estimates a difference of -7.53, with a 95% confidence interval from -11.48 to -3.58 and p < 0.001. This is the trial’s reported primary analysis and should be the main reference for the primary endpoint.

The simple recalculation from posted arm summaries estimates a difference of -7.54, with a confidence interval from -11.45 to -3.63 and p < 0.001. It is an unadjusted reconstruction and does not reproduce the sponsor’s ANCOVA model. Its purpose is to provide a basic check using the reported group estimates and standard errors, not to replace the model-based analysis.

The two estimates are close in direction and magnitude, and the registry record does not flag a discrepancy. If a discrepancy were flagged, the sponsor’s own analysis would take precedence for reporting the trial’s result. In this record, both analyses support the same broad reading of the primary contrast, while the sponsor’s model remains the official reported inferential analysis. Details of the adjustment variables and full model specification are not reported in the registry record, so the recalculation cannot be used to reconstruct those features.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists a primary outcome and eight secondary outcomes, covering pain, total WOMAC score, and responder rates at Day 30 and Day 60. When several outcomes are examined, the chance of at least one apparently striking result arising by chance can increase. Statistical procedures such as a prespecified testing hierarchy or multiplicity adjustment can address aspects of this issue. Whether such procedures were planned or used is not reported in the registry record. The record reports one primary analysis and does not describe an adjustment across the secondary outcomes.

The primary endpoint should therefore remain the main focus when interpreting the trial’s result. Secondary outcomes can add context, especially when they assess related measures or different follow-up times, but unadjusted comparisons should be treated more cautiously than a result protected by a stated multiplicity plan. The registry record does not provide enough information to determine whether a separate protocol or analysis plan specified additional controls.

The primary population is explicitly per protocol. It consists of randomized participants who underwent the assigned treatment, had treatment successfully delivered as intended by the device, and complied with the pain-medication wash-out before baseline. This is a narrower analysis population than all randomized participants. The registry does not report a separate intention-to-treat analysis for the primary endpoint, nor does it explain the reasons participants may have been excluded from the per-protocol population.

Missing-data methods, the amount and pattern of missing outcome data, and any sensitivity analyses for missingness are not reported in the registry record. Those details matter because analyses can depend on assumptions about outcomes that were not observed. The registry also does not report interim analyses or stopping rules. Their absence from the registry entry should be read as unreported information, not evidence that a particular procedure was or was not used.

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 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: pulmonary embolism (1.7%), myocardial infarction (0.8%), acute myocardial infarction (0.8%), lung neoplasm malignant (0.8%).

The safety figures are presented for participants at risk in each group. For serious adverse events, the registry lists 2 affected participants among 121 at risk in the iovera° group and 1 among 59 at risk in the sham group. The death counts are 1 for iovera° and 0 for sham. These are descriptive counts; they do not by themselves establish whether an event was caused by the device or treatment, or whether the groups differ in safety.

The registry’s listed serious-event terms include pulmonary embolism at 1.7%, myocardial infarction at 0.8%, acute myocardial infarction at 0.8%, and lung neoplasm malignant at 0.8%. These terms should be read as the entries recorded for serious adverse events, not as evidence that every listed event was related to the intervention. The record does not provide enough information in these summary figures to assess event timing, severity beyond the serious classification, attribution, or individual clinical circumstances.

Other adverse events are listed for 121 of 121 participants at risk in the iovera° group and 59 of 59 at risk in the sham group. These counts are distinct from the serious-event counts. The registry summaries do not replace a detailed safety review and should not be used alone to make judgments about individual risk or treatment choice.

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

The primary result describes a difference in average change in patient-reported WOMAC pain score between the randomized treatment groups over the baseline-to-Day 30 interval. Both group estimates moved in the direction the registry defines as improvement, and the ANCOVA estimate favors a greater mean reduction in the iovera° group. Its confidence interval gives a range of plausible values for that group difference under the reported analysis and assumptions.

That finding is specific to the primary endpoint, the time point, and the per-protocol population. It does not state that all participants improved, nor does a group average show how outcomes varied from person to person. It also does not establish how long any observed difference persisted after Day 30. The registry includes Day 60 secondary measures, but the primary endpoint itself is measured at Day 30.

The result does not by itself establish clinical importance. Statistical evidence about a difference and the importance of that difference to patients are related but distinct questions. The registry does not report a threshold for a clinically meaningful change in WOMAC pain score. It also does not report enough information about missing data, the detailed ANCOVA specification, or multiplicity handling to resolve every analytic concern.

Nor does a trial result answer every question about the intervention. The posted outcomes do not establish effects on outcomes that were not measured, safety beyond the reported follow-up, or results in populations not represented by the trial. The serious adverse event counts are descriptive and do not establish causality. The appropriate reading is limited to the evidence recorded: estimates from a randomized, quadruple-masked comparison, analyzed in the stated per-protocol population, for the listed outcomes and follow-up times. These statistics are not medical advice and do not determine an individual’s care.

18. Why This Trial Matters Statistically

This trial illustrates why a clinical result should be read through its estimand, analysis population, and uncertainty rather than through a p-value alone. The primary outcome is a patient-reported pain score, the comparison is expressed as a difference in adjusted group means, and the confidence interval communicates precision around that estimate. Those pieces together make the result more interpretable than a significance label by itself.

It also illustrates the importance of distinguishing the sponsor’s model-based analysis from a simple calculation using group summaries. The registry reports an ANCOVA estimate, while the recalculation is unadjusted. Their close alignment is a useful consistency check, but they are not interchangeable analyses. The registry’s report remains the basis for the primary inferential result.

Another statistical lesson is that planning calculations are conditional illustrations, not retrospective measures of success. The per-arm examples show how the required sample size changes when the targeted effect is smaller, under stated assumptions. They cannot recover the trial’s original design rationale, which is not reported in the registry record. Likewise, secondary findings must be interpreted in light of the number of outcomes considered and the lack of a reported multiplicity procedure.

Finally, a trial’s headline conclusion can depend on who is included in the analysis. Here the primary result is per protocol, with criteria concerning treatment delivery and medication wash-out. That definition is essential to interpreting what population the estimate represents. The record leaves important details unreported, including missing-data handling and the full model specification. A careful statistical reading recognizes both the information the registry does provide and the uncertainty that remains.

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.

Several limitations are specific to the information recorded for this trial. The primary analysis is per protocol, with exclusions tied to successful delivery of assigned treatment and compliance with pain-medication wash-out. The registry does not report a separate intention-to-treat primary result or describe the numbers and reasons for exclusions from the per-protocol population. The estimate therefore applies directly to the stated analysis population, and its relationship to outcomes among all randomized participants cannot be assessed from the record alone.

The registry identifies ANCOVA but does not report the covariates, model diagnostics, or other details needed to reproduce the primary analysis. It also does not describe missing outcome data or methods for handling them. A simple recalculation can use the posted summaries, but cannot recover these model and data-handling details. The record does not provide a clinically meaningful threshold for the WOMAC pain subscale, limiting interpretation of the practical importance of the estimated difference.

The primary endpoint is measured at Day 30. Although the registry lists secondary outcomes at Day 60, the primary result does not establish persistence beyond its own assessment time. The available safety summaries are counts and listed event terms, without enough detail to determine causality or characterize individual cases. The registry record also does not report the original sample-size assumptions, interim analyses, or multiplicity procedures. These omissions limit assessment of design rationale and the inferential status of secondary findings; they should not be filled in by assumption.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Study to Evaluate the Iovera° Device for Temporary Relief From Knee Pain — NCT02260921.
• Registry record last updated 2024-01-24; status last verified 2024-01.
• Results first posted 2020-12-31.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

The registry describes a completed, randomized, parallel-group, quadruple-masked, prospective, multicenter study of the iovera° device versus sham treatment for knee osteoarthritis pain. Enrollment is listed as 180. The primary outcome is change from baseline to Day 30 in WOMAC pain subscale score, analyzed using ANCOVA in a per-protocol population.

The sponsor-reported difference in least-squares means is -7.53, with a 95% confidence interval from -11.48 to -3.58 and p < 0.001. Negative change indicates improvement, and the reported contrast estimates a greater mean reduction in the iovera° group. The registry also lists secondary measures at Day 30 and Day 60 and provides summary safety counts. Details about missing-data methods, multiplicity handling, the full model specification, and the original sample-size assumptions are not reported in the registry record.