A Study to Evaluate the Safety and Efficacy of Topically Applied TV-45070 (Ointment) in Participants With Primary Osteoarthritis (OA) Affecting a Single Knee: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study to Evaluate the Safety and Efficacy of Topically Applied TV-45070 (Ointment) in Participants With Primary Osteoarthritis (OA) Affecting a Single Knee (NCT02068599), a randomized phase 2 study. The primary outcome is Change From Baseline to Last 5 Days of Treatment in the Average Evening Pain Intensity In the Target Knee When Walking on a Flat Surface Using a Mixed Model for Repeated Measures (MMRM).

2. Clinical Question

3. Trial Design

The registry record describes a phase 2, randomized, double-blind, placebo-controlled study with a parallel-group design. It enrolled 389 participants with osteoarthritis of the knee. The study was completed. The recorded start date is 2014-04-14, and the primary completion date is 2015-04-06. Those dates identify the recorded study timeline, but they do not establish details of the analysis conduct or reporting process.

Participants were assigned to TV-45070 4%, TV-45070 8%, or placebo. Each ointment was applied topically to the target knee twice daily from day 1 through day 28. The registry names the sponsor as Teva Branded Pharmaceutical Products R&D, Inc. Randomization and double masking can reduce certain sources of bias when allocation and masking are implemented successfully. The registry description alone does not report how allocation was generated or concealed, how masking was maintained, or whether masking was assessed.

The primary endpoint was change in average evening pain intensity while walking on a flat surface, measured from baseline to the last 5 days of treatment. Its analysis population was the full analysis set, with eligibility based on treatment exposure and availability of baseline and post-baseline efficacy assessments. The registry describes the endpoint analysis as a mixed model for repeated measures and states the model factors and covariate. The number enrolled overall is not identical to the number included in each primary comparison: the analysis counts were 121 for TV-45070 4%, 123 for TV-45070 8%, and 120 for placebo.

The registry record does not report the trial’s original sample-size justification or the assumptions used to choose enrollment. It also does not report a complete statistical analysis plan, the randomization procedure, or the details of how missing observations were handled. These omissions limit what can be inferred about design decisions and analysis procedures beyond the items explicitly described.

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.

Before assignment: After stratification by R1150W polymorphism status: - homozygous minor allele (positive, AA), - heterozygous (positive, AG), and - homozygous common allele (negative, GG), participants were randomly assigned by interactive response technology (IRT) to receive treatment in 1 of 3 treatment groups in a 1:1:1 ratio.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The full analysis set (FAS) include all patients in the intent to treat (ITT) population who receive at least 1 dose of study drug and have at least 1 post baseline efficacy assessment. Both baseline and treatment values must be available for a participant to be included.

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: Randomized participants

6. Primary Endpoint

The registry lists the primary outcome as Change From Baseline to Last 5 Days of Treatment in the Average Evening Pain Intensity In the Target Knee When Walking on a Flat Surface Using a Mixed Model for Repeated Measures (MMRM), measured over Baseline (day -5 to day -1), Last 5 days of treatment (day 24 to day 28).

The primary endpoint is change from baseline in average evening pain intensity in the target knee when walking on a flat surface. It uses WOMAC Question 1, the first item in the WOMAC pain domain. Participants recorded their response in a study diary, rating average pain upon walking since the last assessment or over the past 12 hours. Each item is scored from 0, no pain, to 100 mm, worst pain. The measurement window compares baseline, day -5 to day -1, with the last 5 days of treatment, day 24 to day 28.

The registry describes the WOMAC as a patient-reported questionnaire used to assess pain, stiffness, and physical function in knee osteoarthritis. A single pain item focuses this endpoint on a specific experience rather than combining different aspects of the condition into one score. Change from baseline captures the direction and amount of movement in the score over the specified period. For this endpoint, a negative change indicates improvement in pain. The treatment contrasts are presented as least-squares mean differences from placebo, so they express how the modeled change differs between each active-strength group and the placebo group.

Repeated measurements can contribute information across the assessment period rather than relying only on a single follow-up observation. The registry says the primary analysis used a mixed model for repeated measures. The record does not describe the clinical importance threshold for a change in this score, so the observed differences should not be characterized as clinically important or unimportant on the basis of these data alone.

7. Results Posted in the Registry

• TV-45070 4%: mean -20.56 versus -24.82 on control; difference 4.26 (95% CI -1.10 to 9.62), standardized effect d = 0.20; z-test p = 0.119.
• TV-45070 8%: mean -23.08 versus -24.82 on control; difference 1.74 (95% CI -3.60 to 7.08), standardized effect d = 0.08; z-test p = 0.523.

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 to Last 5 Days of Treatment in the Average Daily WOMAC Pain Subscale Score In the Target Knee Using a Mixed Model for Repeated Measures

• 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:
  • TV-45070 4%: mean -99.67 versus -117.53 on control; difference 17.86 (95% CI -8.05 to 43.77), standardized effect d = 0.17; z-test p = 0.177.
  • TV-45070 8%: mean -108.52 versus -117.53 on control; difference 9.01 (95% CI -16.81 to 34.83), standardized effect d = 0.09; z-test p = 0.494.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between TV-45070 4% and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between TV-45070 8% and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline to Last 5 Days of Treatment in the Average Morning Pain Intensity In the Target Knee When Walking on a Flat Surface Using a Mixed Model for Repeated Measures (MMRM)

• 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:
  • TV-45070 4%: mean -19.84 versus -23.45 on control; difference 3.61 (95% CI -1.83 to 9.05), standardized effect d = 0.17; z-test p = 0.193.
  • TV-45070 8%: mean -21.39 versus -23.45 on control; difference 2.06 (95% CI -3.36 to 7.48), standardized effect d = 0.10; z-test p = 0.456.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between TV-45070 4% and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between TV-45070 8% and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline (Randomization Visit) to the Week 4 Visit in the WOMAC Physical Function Subscale Score for the Target Knee Using a Mixed Model for Repeated Measures

• 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:
  • TV-45070 4%: mean -372.88 versus -396.39 on control; difference 23.51 (95% CI -74.56 to 121.58), standardized effect d = 0.06; z-test p = 0.638.
  • TV-45070 8%: mean -446.79 versus -396.39 on control; difference -50.40 (95% CI -147.98 to 47.18), standardized effect d = -0.13; z-test p = 0.311.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between TV-45070 4% and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between TV-45070 8% and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes address other dimensions of pain and knee-related experience, including average daily WOMAC pain, morning pain while walking on a flat surface, physical function, stiffness, pain quality, response thresholds, and global assessments. The registry lists multiple secondary measures, but numerical results are not reported in the registry record for every listed measure. Conclusions about the full set of secondary outcomes therefore cannot be drawn from the available numeric results alone.

Among the secondary outcomes with numerical results reported in the registry record, the estimates do not form a consistent pattern favoring either active strength over placebo. The reported comparisons for daily WOMAC pain and morning pain have confidence intervals that include zero for both active strengths. The same is true for the reported physical-function comparisons. These findings broadly align with the primary result in that they do not establish a clear separation from placebo in the posted model-based comparisons. The endpoints measure different features and scales, however, so they should not be treated as interchangeable confirmations of the primary outcome.

Secondary measures are generally interpreted with less weight than a prespecified primary endpoint, particularly when many outcomes and contrasts are examined. If no adjustment for multiple testing is applied, the chance of obtaining at least one apparently unusual result across many tests can increase. The registry record does not report whether multiplicity adjustment was planned or used. That uncertainty argues for restraint in emphasizing isolated secondary findings, especially where results are incomplete or not numerically reported.

The secondary results should be read as supporting context rather than as independent proof of a treatment effect or its absence. A confidence interval that includes zero is not evidence that two groups are equivalent, and the lack of numerical reporting for some outcomes leaves their direction and precision unknown. The overall interpretation remains anchored in the stated primary endpoint and the sponsor’s primary mixed-model comparisons.

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

• Change From Baseline to Last 5 Days of Treatment in the Average Daily WOMAC Pain Subscale Score In the Target Knee Using a Mixed Model for Repeated Measures
• Change From Baseline to Last 5 Days of Treatment in the Average Morning Pain Intensity In the Target Knee When Walking on a Flat Surface Using a Mixed Model for Repeated Measures (MMRM)
• Change From Baseline (Randomization Visit) to the Week 4 Visit in the WOMAC Physical Function Subscale Score for the Target Knee Using a Mixed Model for Repeated Measures
• Change From Baseline (Randomization Visit) to the Week 4 Visit in the WOMAC Stiffness Subscale Score for the Target Knee Using a Mixed Model for Repeated Measures
• Percentage of Participants With a >=30% and a >=50% Response in Average Evening Pain Intensity of WOMAC Question 1 in the Target Knee During the Last 5 Days of Treatment Compared With Baseline
• Change From Baseline (Randomization Visit) to the Week 4 Visit in the Pain Quality Assessment Scale - Revised (PQAS-R) for the Target Knee Using a Mixed Model for Repeated Measures
• Participants' Global Assess of Treatment as Measured by the Patient Global Impression of Change (PGIC) at Weeks 2 and 4 Using a Mixed Model for Repeated Measures (MMRM)
• Change From Baseline in the Patient Global Assessment (PGA) Scores at Weeks 2 and 4 Using a Mixed Model for Repeated Measures (MMRM)

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is continuous: it is a numerical score, and the result is expressed as a modeled mean change. The registry reports least-squares means from a mixed model for repeated measures. A least-squares mean is a model-based group estimate that accounts for the terms included in the model; it is not necessarily the same as a simple arithmetic average of the observed scores. The registry does not report all implementation details, such as the covariance structure used for repeated measurements.

What does the repeated-measures model do?

General: repeated-measures models analyze observations collected from the same participant at multiple times while accounting for the relationship among those observations. This can use information from more than one follow-up assessment and can accommodate unequal numbers of recorded observations under the model’s assumptions. The registry says the primary model included week, treatment, study center, and treatment-by-week interaction as fixed factors; baseline average evening WOMAC Question 1 score as a covariate; and patient as a random factor. A fixed factor represents a modeled feature whose effects are estimated for the analysis. A random factor represents participant-level variation in the model.

The treatment-by-week interaction allows the modeled treatment contrast to vary by week rather than requiring a single common treatment difference at every time. Including baseline score as a covariate adjusts the modeled comparison for the starting value of this same pain measure. Study center and week are also named in the registry’s description. The record does not report further modeling choices, such as the covariance structure, degrees-of-freedom method, or exact handling of observations missing at particular visits.

How should the treatment contrast be read?

The reported contrast is the least-squares mean difference from placebo. For the primary endpoint, the contrast is positive when the modeled change in the active group is less negative than the modeled change in placebo. Since negative change indicates improvement on this pain scale, a positive contrast points toward less reduction in the active group relative to placebo for this measure. This is a description of the direction of the estimate, not a clinical judgment about importance.

The sponsor’s reported primary contrasts were 4.26 for TV-45070 4% versus placebo and 1.74 for TV-45070 8% versus placebo. The corresponding 95% confidence intervals were -1.13 to 9.66 and -3.62 to 7.11. Both intervals cross zero. The registry’s test results are reported as p-values, which quantify how compatible the observed data are with a specified null hypothesis under the analysis model. A p-value does not give the probability that the null hypothesis is true, nor does it measure the probability that a finding occurred by chance in a general, assumption-free sense.

What do the recalculated summaries add?

The unadjusted recalculations use the posted group summaries to form approximate differences and confidence intervals. They are not a replacement for the sponsor’s repeated-measures model. The calculations use approximate standard deviations inferred from the reported standard errors and group counts; they do not reproduce the model’s adjustment for week, center, baseline, or within-participant repeated measurements. For the primary endpoint, the recalculated differences are 4.26 and 1.74, with intervals of -1.097 to 9.617 and -3.597 to 7.077. They are close to, but not identical with, the sponsor-reported intervals.

General: a confidence interval describes a range of estimates compatible with the data and statistical model at the stated confidence level. It communicates precision as well as direction. An interval that includes zero does not rule out a null difference, and its width indicates that estimates across a range remain compatible with the observations. The 95% label refers to the long-run coverage property of the interval procedure under its assumptions; it is not a 95% probability that this particular interval contains the true value.

Why can model-based and simple estimates differ?

General: model-based estimates and unadjusted estimates can differ because they use different information and assumptions. A repeated-measures model accounts for the specified time structure and covariates, while a summary-statistic calculation treats the group summaries as the basis for comparison. The recalculated standard deviations are approximate, and the calculation does not recover participant-level data. For these reasons, the sponsor’s reported mixed-model analysis is the principal source for the trial’s primary comparison; the recalculations are a supplementary check on scale and precision.

The registry reports a full analysis set that requires at least one dose, at least one post-baseline efficacy assessment, and available baseline and treatment values. General: restricting analysis to participants with observed information can affect the composition of the analyzed groups if inclusion is related to prognosis or outcome. Repeated-measures models may use available observations, but the registry record does not say how missingness was assumed or whether sensitivity analyses were conducted. It is therefore not possible to assess from this record alone how robust the findings are to different missing-data assumptions.

The record also does not report a complete prespecified analysis plan or explain how testing across multiple endpoints and treatment comparisons was controlled. This matters because repeated testing can increase the chance of at least one nominally unusual result. The primary endpoint should therefore be distinguished from the many secondary measures, and secondary findings should be interpreted with appropriate caution.

11. Confidence Intervals and Precision

The sponsor-reported 95% confidence interval for the TV-45070 4% comparison extends from -1.13 to 9.66; for TV-45070 8%, it extends from -3.62 to 7.11. Each interval includes zero, the value corresponding to no estimated mean difference from placebo. The intervals also include values on both sides of zero, so the primary estimates do not pin down the direction of a difference with high precision.

The endpoints are measured on the WOMAC pain-item scale, for which the registry gives a range from 0 to 100 mm. In this trial, negative change from baseline indicates improvement. Thus, the positive treatment contrasts indicate that the modeled changes in the active groups were less negative than the placebo change at the point estimates. The confidence intervals show that the data are also compatible with a small difference in the opposite direction, as well as a range of positive differences. The registry does not report a threshold for a clinically important change, so interval limits cannot be classified as clinically meaningful or trivial from this record alone.

The sponsor’s intervals are the relevant precision estimates for the repeated-measures analysis. The unadjusted recalculated intervals are similar but not identical, because they are derived from summary statistics and approximate standard deviations rather than the full model. That proximity is reassuring as a basic consistency check, but it does not make the recalculation equivalent to the sponsor’s analysis. Differences in model structure and assumptions can affect interval limits.

General: an interval’s width reflects uncertainty under the chosen analysis, including the amount and variability of information available. More narrow intervals generally indicate greater statistical precision, while wider intervals leave more plausible values unresolved. Precision is not the same as validity: an estimate can be precise while still subject to bias or limitations in design, measurement, or analysis. These intervals describe the primary endpoint comparison for this study and do not automatically generalize to other outcomes, time points, or populations.

12. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The planning figures are participants per arm for the continuous-outcome comparisons in this trial; they are not total event counts. The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect. The planning illustrations are based on the observed effect, not on the trial’s original design assumptions; those original assumptions are not reported in the registry record.

The 80% power column gives the illustrative number of participants per arm needed for an 80% chance of detecting the specified effect under the listed assumptions, if that effect and the assumptions were correct. The 90% power column makes the same kind of calculation for a 90% chance. These are design-planning quantities: they describe the operating characteristics of a hypothetical future study, not what happened in this completed trial.

For example, planning for 100% of the observed primary contrast gives 390 participants per arm for 80% power and 522 participants per arm for 90% power for the 4% comparison. For the 8% comparison, the corresponding figures are 2,336 and 3,128 participants per arm. Planning for 75% or 50% of the observed effect requires more participants per arm than planning for the full observed effect. Smaller target effects are harder to distinguish from background variation, so they generally require larger sample sizes under otherwise similar assumptions.

These are illustrations only, and they should not be read as a retrospective judgment about whether the completed trial was adequately designed. They depend strongly on the observed effect, which can be uncertain, and the normal-approximation calculation does not reproduce the trial’s repeated-measures analysis. This is not observed power. The registry record does not report the original sample-size justification or its planning assumptions.

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 = 4.260; pooled standard deviation σ = 21.214.
2. n = 2 × (1.96 + 0.842)² × 21.214² / 4.260² = 389.3, rounded up to 390 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 <- 4.26                      # observed difference in means
sigma <- 21.2141873858867                     # 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(2068599)
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 = 390 (80% power), 522 (90% power)
 75% of observed effect: n per arm = 693 (80% power), 927 (90% power)
 50% of observed effect: n per arm = 1,558 (80% power), 2,085 (90% power)
power.t.test: 390.3 
Simulated power at n = 390 per arm: 0.803 (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-reported primary analyses use a mixed model for repeated measures and report least-squares mean differences from placebo. For TV-45070 4%, the estimate was 4.26 with a 95% confidence interval from -1.13 to 9.66. For TV-45070 8%, it was 1.74 with a 95% confidence interval from -3.62 to 7.11. These are the trial’s reported model-based comparisons and should be treated as the primary analysis results.

The simple recalculations from the posted summary statistics return the same point estimates, 4.26 and 1.74, but produce approximate confidence intervals of -1.097 to 9.617 and -3.597 to 7.077. The modest differences in interval limits are expected because the recalculation is unadjusted and uses approximate standard deviations inferred from standard errors. It does not replicate the repeated-measures model or its adjustment terms.

The registry’s sponsor-reported p-values are 0.121 and 0.523. The recalculated unadjusted p-values are 0.119 and 0.523, respectively. The small differences are consistent with the distinct methods; neither should be treated as a correction of the other. There is no material discrepancy flagged between the sponsor’s results and the recalculations. For interpretation, the sponsor’s model-based results take priority because they reflect the analysis method reported for the primary endpoint. The simpler calculations are best viewed as a supplementary consistency check, not as an alternative primary analysis.

15. Multiplicity, Missing Data and Analysis Populations

The trial assessed a primary endpoint alongside multiple secondary outcomes and compared two active strengths with placebo. Each additional outcome or comparison creates another opportunity for a result to appear unusual under a null hypothesis, particularly when tests are considered together. Statistical methods that control multiplicity can address this issue, but they may affect thresholds, intervals, or the interpretation of individual tests.

The registry record does not report whether the primary analysis was protected by a testing hierarchy, whether secondary tests were adjusted for multiplicity, or what family of hypotheses was considered. It also does not report an overall statistical analysis plan sufficient to establish the ordering or confirmatory status of the secondary outcomes. The posted p-values should therefore be read as the results of the reported comparisons, not assumed to have a particular familywise error interpretation.

The primary endpoint analysis population is described as the full analysis set. It included participants in the intent-to-treat population who received at least one dose and had at least one post-baseline efficacy assessment, with baseline and treatment values available. The registry reports the analysis counts for the primary endpoint, but does not give a full account of reasons for exclusion, missing observations by visit, or how missing data were handled in the model. It also does not report sensitivity analyses under alternative missing-data assumptions.

The primary analysis used a mixed model for repeated measures, and such models can use available repeated observations. General: the interpretation of a model with missing observations depends on assumptions about why values are missing and how missingness relates to observed or unobserved outcomes. The registry record does not state those assumptions or provide enough information to assess them. This is a reporting limitation; it does not by itself establish that the analysis was inappropriate.

The original sample-size rationale, interim-analysis plan, and trial-specific significance threshold are not reported in the registry record. Their absence prevents assessment of whether enrollment was selected to provide a planned level of precision for the primary comparison or whether any planned monitoring or testing procedures affected the final analysis.

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: acute myocardial infarction (0.8%), influenza (0.8%).

The registry reports serious adverse events affecting 1 participant in the TV-45070 4% group, 0 in the TV-45070 8% group, and 1 in the placebo group. The corresponding numbers at risk were 129, 128, and 130. Deaths were reported as 0 in each group. These are counts, not estimates of comparative risk adjusted for exposure time or other factors.

The listed serious adverse-event terms were acute myocardial infarction and influenza, each reported as 0.8%. The registry information does not assign those listed terms to a specific treatment group in the registry record, so they should not be attributed to one. The record also reports other adverse events affecting 6 participants in each active-strength group and 9 in the placebo group, among 129, 128, and 130 participants at risk, respectively. Those counts are distinct from the serious-event counts.

Safety counts require cautious interpretation. Small numbers of events can fluctuate, and raw counts do not establish whether a treatment caused an event or whether groups differ reliably. The registry information does not provide event timing, exposure-adjusted rates, severity details beyond the serious-event classification, or a comprehensive account of event terms in this summary. These figures describe the posted record and should not be used alone to make causal or clinical conclusions.

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

The primary result describes modeled differences in change in average evening pain intensity while walking on a flat surface, comparing each TV-45070 strength with placebo during the stated treatment period. The point estimates were positive, and both sponsor-reported confidence intervals included zero. The posted analysis therefore does not establish a clear difference from placebo on this specific primary endpoint. It also does not show that the treatments and placebo are equivalent: the intervals retain a range of possible differences.

The endpoint is one patient-reported pain item, measured at a defined time window. It cannot represent every aspect of knee osteoarthritis, every daily activity, or outcomes beyond the assessment period. Other measures in the registry address function, stiffness, pain at another time of day, and patient global assessments, but not all have numerical results reported. The primary result should not be extended to outcomes that were not assessed or numerically reported.

The study was described as phase 2 and included 389 enrolled participants overall. The primary analysis used smaller analysis-set counts because it required treatment exposure and available baseline and post-baseline efficacy information. The result applies to the trial’s analysis population and setting; it does not automatically apply to every person with knee osteoarthritis or to other treatment schedules.

Statistical uncertainty is only one consideration. The registry record does not provide a threshold for clinical importance, a complete account of missing-data assumptions, or the trial’s original sample-size rationale. Consequently, the estimates should be interpreted as the reported statistical comparisons rather than as a definitive assessment of practical importance. The safety counts are also descriptive and do not establish causation.

In short, the posted results show no clear separation from placebo in the reported primary model-based comparisons, while leaving uncertainty about the range of effects compatible with the data. They do not demonstrate equivalence, establish the absence of effects on other outcomes, or support conclusions beyond the measured participants, outcomes, and treatment period.

18. Why This Trial Matters Statistically

This trial illustrates why an estimated treatment difference should be read together with its confidence interval. The primary point estimates alone give a direction and scale, but the intervals show that a range of values remains compatible with the data. Here, both sponsor-reported primary intervals include zero, so the estimates do not precisely distinguish the active groups from placebo on the stated outcome.

It also illustrates the distinction between a trial’s reported model and a simple summary-statistic comparison. The registry describes a repeated-measures model with baseline adjustment, study center, week, treatment, and a treatment-by-week interaction. Unadjusted recalculations from group summaries are useful as a rough check, but they do not reproduce that analysis. Treating the two approaches as interchangeable would conceal the role of model assumptions and repeated observations.

The endpoint itself matters. This comparison concerns a specific WOMAC pain item, at a specified time of day and activity, over the last 5 days of treatment. It is not a global measure of symptoms or function. Knowing precisely what is measured helps prevent a narrow result from being generalized to the entire clinical condition.

Finally, the record highlights the importance of reporting decisions that shape interpretation: original sample-size assumptions, missing-data handling, multiplicity procedures, and complete numerical secondary results. These details are not reported in the registry record. Their absence limits how fully readers can evaluate the intended precision, the robustness of the analysis, and the evidential weight of secondary findings. Statistical interpretation depends not just on a point estimate, but also on design, analysis, reporting, and uncertainty.

19. Limitations

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

The primary outcome is a self-reported pain item tied to walking on a flat surface. It provides a focused measure, but it does not cover all pain contexts or the full experience of knee osteoarthritis. The registry record does not provide a threshold for a clinically important change, which limits interpretation of the numerical size of the contrasts.

The primary analysis population required at least one dose and available baseline and post-baseline efficacy assessments. The analysis counts are therefore not the same as overall enrollment. The registry record does not report detailed reasons for exclusion, missingness by visit, or sensitivity analyses addressing missing-data assumptions. This leaves uncertainty about how the analysis might depend on the availability of outcome data.

The record describes the repeated-measures model but does not report all model implementation details. It also does not report the original sample-size justification, the complete statistical analysis plan, or multiplicity procedures. Without those details, it is difficult to judge the intended precision, the status of secondary analyses, and the handling of the multiple comparisons.

Numerical results are not reported in the registry record for every listed secondary outcome. This makes the overall secondary-outcome pattern incomplete. Safety information is also presented as counts in the record summary; the available details do not establish exposure-adjusted rates or causal attribution. Finally, the findings apply to the specified study population, topical formulations, target knee, and treatment period. The registry information does not establish whether the results would be similar with other durations, application schedules, or populations.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Study to Evaluate the Safety and Efficacy of Topically Applied TV-45070 (Ointment) in Participants With Primary Osteoarthritis (OA) Affecting a Single Knee — NCT02068599.
• Registry record last updated 2021-11-09; status last verified 2021-11.
• Results first posted 2018-10-23.
• 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 record describes a completed phase 2 randomized, double-blind, parallel-group study of TV-45070 4% ointment, TV-45070 8% ointment, and placebo in participants with primary osteoarthritis affecting a single knee. Overall enrollment was 389. Treatment was applied to the target knee twice daily from day 1 through day 28.

The primary endpoint was change in average evening pain intensity while walking on a flat surface, measured using WOMAC Question 1. The sponsor-reported model-based differences from placebo were 4.26 for the 4% group and 1.74 for the 8% group; both 95% confidence intervals included zero. The registry also reports secondary outcome measures and safety counts, but numerical findings are not available for every listed secondary outcome.

The original sample-size justification, multiplicity procedures, and detailed missing-data assumptions are not reported in the registry record. The primary model-based results are the central evidence for interpreting the trial’s stated primary question.