Patient-Reported Outcomes in Evaluating Lorecivivint (SM04690) for Moderate to Severe Knee Osteoarthritis (STRIDES-1): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Patient-Reported Outcomes in Evaluating Lorecivivint (SM04690) for Moderate to Severe Knee Osteoarthritis (STRIDES-1) (NCT04385303), a randomized phase 3 study. The primary outcome is Change From Baseline OA Pain in the Target Knee as Assessed by the Weekly Average of Daily Pain Numeric Rating Scale (NRS) at Week 12.

2. Clinical Question

This question is about a difference between assigned groups, not simply whether pain scores changed over time within either group. A change within one arm can reflect many influences, including the course of symptoms, study participation and the injection procedure. The randomized comparison is the relevant contrast for assessing whether the observed change differed between the lorecivivint and vehicle groups. The registry record does not report a threshold defining what size of between-group difference would be clinically important, so statistical estimates should not be treated as establishing clinical importance.

3. Trial Design

STRIDES-1 was a phase 3, multicenter, randomized, parallel-group study of lorecivivint and vehicle for moderately to severely symptomatic knee osteoarthritis. The registry record describes the study as double-blind and placebo-controlled, and lists triple masking. It was completed. The record lists a planned enrollment of 496, a start date of 2020-05-26 and a primary completion date of 2021-09-08.

Participants were assigned to receive a single injection into the target knee. The intervention description identifies lorecivivint as an intra-articular dose of 0.07 mg in 2 mL. The arm descriptions state that both injections were administered by a healthcare professional on Day 1. The registry calls the comparator arm Vehicle; its brief study description calls the study placebo-controlled. The treatment schedule described in the record is a single injection, while the primary outcome was assessed at Week 12 and the overall study title specifies 28 weeks.

The primary outcome was change from baseline in weekly average daily pain on the target-knee pain Numeric Rating Scale at Week 12. The registry record also lists secondary outcomes involving pain at Week 24, WOMAC physical function at Week 12 and Week 24, and Patient Global Assessment at Week 12 and Week 24. The completed record lists 12 outcome measures and 12 analyses, although the clinical detail available for interpretation depends on the particular outcomes with posted numerical results.

For the primary outcome, the Full Analysis Set included randomized participants who received a study injection. The registry says observed data were analyzed as randomized without imputation. The endpoint-level analysis counts are 213 in the Vehicle arm and 211 in the Lorecivivint arm. These analysis counts should not be confused with planned enrollment: they refer to participants included in the posted primary endpoint analysis, not a recalculation of enrollment or of the number randomized.

The registry record does not report the trial’s original sample-size justification, the allocation ratio intended in the protocol, or the detailed statistical analysis plan. It also does not report the specific adjustment variables or covariance structure used in the mixed-model analysis. Those details cannot be inferred from the fact that the study was randomized or from the name of the reported method.

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: Full Analysis Set includes all subjects who were randomized and received a study injection. Subjects' observed data were analyzed as randomized without imputation.

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: Full Analysis Set

6. Primary Endpoint

The registry lists the primary outcome as Change From Baseline OA Pain in the Target Knee as Assessed by the Weekly Average of Daily Pain Numeric Rating Scale (NRS) at Week 12, measured over Baseline and Week 12.

The primary endpoint measured change from baseline to Week 12 in the weekly average of daily pain ratings for the target knee. Participants rated their average knee pain over the previous 24 hours using an 11-point Numeric Rating Scale, with 0 indicating no pain and 10 representing the worst possible pain. The outcome is therefore a continuous, patient-reported measure: each participant contributes a score, and the group results are expressed as least-squares means of change.

Change from baseline focuses the comparison on movement in scores over the follow-up period rather than on the Week 12 score alone. A negative mean change indicates a lower reported pain score relative to baseline. The principal statistical question is whether the average change differed between randomized groups, not whether either group had a change considered meaningful on its own. The posted group estimates are -2.15 for Vehicle and -2.22 for Lorecivivint; the reported between-group mean difference is -0.07.

Patient-reported pain is relevant because pain is experienced by the participant and may not be fully represented by clinical observations alone. Repeated daily ratings, summarized as a weekly average, can characterize pain over more than one isolated report. That measurement approach does not eliminate limitations such as variation in individual reporting or incomplete observations. The registry describes the scale and analysis population, but does not report a minimal clinically important difference for this endpoint. As a result, the statistical estimate alone does not establish whether a difference would matter to participants.

7. Results Posted in the Registry

• Lorecivivint: mean -2.22 versus -2.15 on control; difference -0.07 (95% CI -0.46 to 0.32), standardized effect d = -0.03; z-test p = 0.724.

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 OA Pain in the Target Knee as Assessed by the Weekly Average of Daily Pain Numeric Rating Scale (NRS) at Week 24

• 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:
  • Lorecivivint: mean -2.26 versus -2.31 on control; difference 0.05 (95% CI -0.34 to 0.44), standardized effect d = 0.03; z-test p = 0.801.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Lorecivivint and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline OA Function in the Target Knee as Assessed by Western Ontario and McMaster Universities Osteoarthritis Index (WOMAC) Physical Function Subscore (WOMAC Function) at Week 12

• 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:
  • Lorecivivint: mean -20.29 versus -22.00 on control; difference 1.71 (95% CI -2.27 to 5.69), standardized effect d = 0.08; z-test p = 0.399.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Lorecivivint and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline OA Function in the Target Knee as Assessed by Western Ontario and McMaster Universities Osteoarthritis Index (WOMAC) Physical Function Subscore (WOMAC Function) at Week 24

• 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:
  • Lorecivivint: mean -20.60 versus -21.91 on control; difference 1.31 (95% CI -2.93 to 5.55), standardized effect d = 0.06; z-test p = 0.545.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Lorecivivint and the control. The interval gives the range of effects that remain compatible with the data.

The numerical secondary results cover pain at Week 24 and WOMAC physical function at Week 12 and Week 24. Across these outcomes, the sponsor-reported comparisons do not establish a clear, consistent separation between Lorecivivint and Vehicle. Their confidence intervals include zero, and the estimates vary in direction and size. This overall pattern is broadly compatible with the primary Week 12 pain result, where the estimated between-group difference was also close to zero and the interval included zero.

The registry also lists Patient Global Assessment outcomes at Week 12 and Week 24, but their numerical results are not reported in the registry record. Their absence means that no conclusion about the direction, size or uncertainty of those particular comparisons can be drawn from the numerical results. The listed outcomes should not be treated as if they had the same result as pain or WOMAC merely because they belong to the same trial.

Secondary outcomes can add context by examining other dimensions of the condition or different follow-up times. They do not have the same interpretive role as the designated primary endpoint, which is the central comparison identified in the registry. When many outcomes or time points are examined, the chance of finding a seemingly notable result by chance can rise. Unadjusted secondary p-values do not account for that broader set of comparisons, and a positive-looking result among many tests would therefore need particular caution.

No multiplicity-control strategy is reported in the registry record. Accordingly, secondary results are best viewed as supportive or exploratory evidence rather than as independent confirmation. Their broad pattern does not overturn the primary finding, but neither does it prove that all outcomes are identical between groups. The missing numerical Patient Global Assessment results and the lack of a reported multiplicity plan also limit how comprehensively the full secondary-outcome family can be assessed.

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

• Change From Baseline OA Pain in the Target Knee as Assessed by the Weekly Average of Daily Pain Numeric Rating Scale (NRS) at Week 24
• Change From Baseline OA Function in the Target Knee as Assessed by Western Ontario and McMaster Universities Osteoarthritis Index (WOMAC) Physical Function Subscore (WOMAC Function) at Week 12
• Change From Baseline OA Function in the Target Knee as Assessed by Western Ontario and McMaster Universities Osteoarthritis Index (WOMAC) Physical Function Subscore (WOMAC Function) at Week 24
• Change From Baseline OA Disease Activity as Assessed by Patient Global Assessment at Week 12
• Change From Baseline OA Disease Activity as Assessed by Patient Global Assessment at Week 24

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous: pain is represented by a numerical score, and change from baseline can take a range of values. For a continuous outcome, a group mean describes the average change, while a standard error describes the estimated sampling uncertainty around that mean. The reported arm summaries are least-squares means with standard errors. Least-squares means are model-based estimates; they are not necessarily identical to raw arithmetic averages, particularly when a model accounts for features of the data.

The primary comparison is a mean difference between Lorecivivint and Vehicle. A mean difference retains the measurement scale, so its size is expressed in pain-scale units. The reported value of -0.07 means the estimated mean change in the Lorecivivint group was lower than the estimated mean change in the Vehicle group by 0.07 scale units, according to the reported contrast. The direction needs to be interpreted alongside the scale: lower pain ratings indicate less reported pain, but the estimate is close to zero and has substantial uncertainty relative to its size.

The registry identifies the sponsor’s primary analysis as a Mixed Models Analysis of Mean Difference (Final Values). A mixed model is a general statistical approach that can represent relationships among observations and account for modeled sources of variation. The registry record does not describe the model’s specific terms, covariance structure, handling of repeated measurements, or adjustment variables. It is therefore not possible to reconstruct the sponsor’s model from the method label alone or to assume which baseline or follow-up values were included beyond what is stated.

The registry’s definition of the Full Analysis Set includes randomized participants who received a study injection. It also states that observed data were analyzed as randomized without imputation. In general, analyzing participants as randomized preserves the comparison created by random assignment among those included in the analysis, even if subsequent events affect their observed outcomes. However, the definition excludes randomized participants who did not receive an injection, and the record does not provide a detailed account of how missing Week 12 observations arose or how they were handled beyond the statement that no imputation was used. Missing outcomes can affect the interpretation if their absence is related to pain or group assignment.

The posted recalculation is an unadjusted comparison based on summary statistics, not a recreation of the mixed model. It uses the displayed arm estimates and standard errors to make a simple comparison. The pooled standard deviation is approximate, as indicated in the underlying calculation, and is useful for expressing a standardized effect size but does not substitute for the sponsor’s model. An unadjusted analysis may differ from a model-based result because the model can account for data structure or covariates not represented in simple summary-statistic calculations. The recalculated p-value of 0.724 and the sponsor-reported p-value of 0.703 are therefore not expected to be identical.

A confidence interval describes a range of effect estimates reasonably compatible with the data and the statistical model at the stated confidence level. In repeated use of the same method under its assumptions, intervals constructed at the 95% level would cover the true parameter in 95% of repetitions. It is not correct to say that there is a 95% probability that this particular interval contains the true effect. The primary sponsor-reported interval runs from -0.46 to 0.31, so its values include zero and modest effects in either direction. The interval does not establish that every value inside it is equally plausible, nor does it account for uncertainties not represented by the model.

A p-value is another summary of the data under a statistical model. It describes how unusual an estimate at least as extreme as the observed one would be if the null hypothesis and model assumptions held. It is not an effect size, a measure of clinical importance, or a probability that the finding occurred by chance. A larger p-value does not demonstrate no effect; it indicates that the observed data do not strongly distinguish the estimated contrast from the null under that test. The registry record does not report a prespecified threshold for the primary test in its analysis description, so the p-value should be read together with the reported estimate and interval rather than used alone.

The registered primary outcome is a single Week 12 comparison, but the record also includes other outcomes and time points. Testing multiple endpoints can increase the chance that at least one apparently notable result arises by chance if each is interpreted without adjustment. No multiplicity adjustment strategy is reported in the registry record. Likewise, no interim-analysis plan, stopping boundary, or detailed sequence for testing endpoints is reported. The absence of such details from the registry record does not establish what was or was not in the full protocol; it limits what can be concluded from the record.

Over-dispersion is a general issue for count outcomes, where variability exceeds what a simple count model expects. It is not the central concern for this continuous pain endpoint, whose analysis is based on group means and their uncertainty. More generally, a model should match the outcome type and data structure; a continuous scale, a count of events and a time-to-event outcome require different statistical representations. The adverse-event counts are descriptive safety summaries and should not be interpreted using the primary continuous-outcome model.

11. Confidence Intervals and Precision

The sponsor-reported primary estimate is a mean difference of -0.07, with a 95% confidence interval from -0.46 to 0.31. The interval crosses zero: it contains values corresponding to a small advantage in either direction under the stated contrast. This breadth means the estimate does not pinpoint a single effect with high precision. The p-value, 0.703, is consistent with the interval’s inclusion of zero, but the interval is more useful for seeing the range of effects compatible with the data.

Precision is distinct from whether an estimate is clinically important. A narrow interval can estimate an effect precisely even if the effect is small; a wider interval can leave substantial uncertainty about magnitude and direction. The registry record does not provide a threshold for a clinically important difference on the pain scale. It is therefore not possible to classify the full interval as clinically trivial or clinically meaningful based on a registry-defined threshold.

The recalculation from arm-level summaries gives the same displayed point estimate, -0.07, but a different unadjusted p-value, 0.724. The recalculation uses an approximate pooled standard deviation and does not reproduce the sponsor’s mixed-model analysis. Its uncertainty calculation should be understood as a simple cross-check rather than as a replacement confidence interval for the trial’s primary analysis.

The endpoint analysis counts and standard errors indicate that the estimate is based on substantial groups, but the size of the analysis groups does not by itself guarantee precision. Precision also depends on outcome variability, the size of the between-group contrast, the analysis method and the completeness of the observations. The posted interval is the most direct summary of uncertainty for the sponsor’s primary comparison. It supports a cautious conclusion: the trial’s reported estimate is close to zero, but the interval does not rule out modest differences in either direction.

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 illustrations express sample sizes as participants per arm. They are not totals across both arms and are not counts of observed trial participants. The calculations use a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. They use the observed effect as a starting point and show illustrations for detecting 100%, 75% or 50% of that observed effect. The trial’s original design assumptions and sample-size justification are not reported in the registry record.

The 80% power column describes a planning target: under the stated assumptions, it is the number of participants per arm associated with an 80% chance of detecting the specified effect if that effect were the true one and the assumptions held. The 90% power column gives the corresponding planning target for a higher chance of detection. These are design calculations, not statements about what occurred in STRIDES-1. In particular, they are not observed power and should not be used to infer the probability that the trial’s finding is true.

For a given endpoint, the illustration based on a smaller fraction of the observed effect calls for more participants per arm than the illustration based on the full observed effect. This is a general feature of statistical planning: smaller effects are harder to distinguish from random variation, so more information is needed to detect them with the same power target. The values are conditional on the calculation assumptions and on using the observed effect as a planning reference; an observed estimate is itself uncertain and may not be the effect a future study should target.

The planning values are therefore best read as sensitivity illustrations, not as a recommendation or a retrospective judgment about whether enrollment was adequate. They do not establish the assumptions used when the trial was originally designed, and they do not quantify the probability of a successful result after the fact. The record does not state the original target effect, variance assumptions, planned power, or other design inputs.

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 = -0.070; pooled standard deviation σ = 2.038.
2. n = 2 × (1.96 + 0.842)² × 2.038² / -0.070² = 13,312.0, rounded up to 13,312 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 <- -0.0700000000000003                      # observed difference in means
sigma <- 2.03845355379887                     # 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(4385303)
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 = 13,312 (80% power), 17,821 (90% power)
 75% of observed effect: n per arm = 23,666 (80% power), 31,682 (90% power)
 50% of observed effect: n per arm = 53,248 (80% power), 71,284 (90% power)
power.t.test: 13313 
Simulated power at n = 13,312 per arm: 0.800 (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 a mixed-model comparison of final values. It estimates a mean difference of -0.07, with a 95% confidence interval from -0.46 to 0.31 and p = 0.703. This is the trial’s reported analysis for the primary endpoint and should be kept distinct from a simple recalculation based on the posted arm summaries.

The unadjusted recalculation also gives a mean difference of -0.07, with p = 0.724. It relies on summary estimates and an approximate pooled standard deviation; it does not reproduce the sponsor’s model or its full data structure. Small differences in p-values can arise because the methods use different information or assumptions. The numerical difference between the p-values does not change the overall interpretation of the primary result: both analyses leave the estimated contrast close to zero and do not show a clear separation between groups.

The registry discrepancy flag is false. There is therefore no flagged conflict requiring a different reading of the posted sponsor analysis. The sponsor’s reported result is the appropriate reference for describing what the trial analysis found; the recalculation is supplementary and should not be presented as a corrected or superior estimate. The registry record does not provide enough detail to independently reproduce every element of the mixed-model analysis.

15. Multiplicity, Missing Data and Analysis Populations

The primary endpoint is clearly identified as Week 12 change in target-knee pain, while the registry lists additional outcomes at Week 12 and Week 24. When investigators test several outcomes, time points or contrasts, the opportunity for a low p-value to occur by chance increases unless the analysis plan accounts for multiplicity. The registry record does not report a family-wise error control procedure, a hierarchy for testing outcomes, or another multiplicity strategy. The secondary findings should therefore be read with caution, especially if considered individually.

The registry identifies a mixed-model method for the primary analysis but does not report the complete statistical analysis plan. Specific model terms, covariates, covariance structure, handling of protocol deviations, or a detailed approach to repeated measurements are not reported in the registry record. No interim-analysis plan or stopping rules are reported either. These details matter to a full audit of whether the analysis followed its prespecified plan, but their absence from the registry record is not evidence that such procedures did not exist outside the record.

For the primary analysis population, the record states that the Full Analysis Set comprised randomized participants who received a study injection. Observed data were analyzed as randomized without imputation. This is important context: the stated approach does not fill missing outcomes with modelled or substituted values. However, the registry record does not give a detailed account of missing Week 12 observations, reasons for missingness, or sensitivity analyses examining alternative assumptions. If participants with unavailable pain scores differed systematically from those with observed scores, the estimate could be affected.

The record also does not provide detailed information about adherence, protocol deviations or how such events influenced inclusion in individual analyses. The endpoint analysis counts vary across outcomes, which is consistent with different sets of observations being available for different analyses, but the reasons for those counts are not reported in the registry record. These limitations do not invalidate the posted estimates; they define the questions that cannot be resolved from the registry information alone.

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 2% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: covid-19 (0.8%), cerebrovascular accident (0.4%), cholecystitis chronic (0.4%), hypertension (0.4%), covid-19 pneumonia (0.4%).

The registry records serious adverse events in 1 of 251 participants at risk in the Vehicle group and 4 of 241 participants at risk in the Lorecivivint group. It records other adverse events in 38 of 251 participants at risk in the Vehicle group and 27 of 241 participants at risk in the Lorecivivint group. Deaths are recorded as 1 in the Vehicle group and 0 in the Lorecivivint group. These are descriptive counts, not estimates of comparative risk adjusted for differences in follow-up or other factors.

The serious adverse-event terms listed most often include COVID-19 at 0.8%, followed by cerebrovascular accident, chronic cholecystitis, hypertension and COVID-19 pneumonia, each at 0.4%. The registry record does not establish from these counts whether an event was caused by an injection. Serious events are uncommon in these summaries, so a small number of events can make the comparison unstable. The counts should be interpreted as safety reporting from this trial, not as proof of a causal difference or as a complete account of risks beyond the record.

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

The primary result is an estimate of the difference between randomized groups in average change in target-knee pain at Week 12. The sponsor’s model estimates a mean difference of -0.07, with a 95% confidence interval from -0.46 to 0.31. The point estimate is close to zero, and the interval includes zero. The result does not show a clear between-group difference on this endpoint in the reported analysis.

That interpretation is not equivalent to saying the treatments are the same. A failure to show clear separation can arise when the true difference is small, when estimates are imprecise, or for other reasons. Equivalence or non-inferiority requires a specific design, a prespecified margin and a corresponding analysis; these are not reported in the registry record. The confidence interval narrows the range of differences compatible with the primary analysis, but it does not prove the absence of any effect.

Nor do the within-group decreases in pain establish that either injection caused improvement. Both arms showed negative mean changes, but a within-group comparison does not isolate the contribution of the assigned injection from other influences. The randomized between-group estimate is the relevant comparative measure, and it is close to zero. The posted outcome is patient-reported pain on a defined scale; it does not directly measure every aspect of osteoarthritis or establish effects on outcomes not reported.

The numerical secondary results do not provide a clearly consistent alternative pattern, and the registry lists Patient Global Assessment outcomes without numerical results. Secondary comparisons also require caution because a multiplicity strategy is not reported. Safety counts offer descriptive information about events recorded during the trial, but they do not by themselves show that an event was caused by treatment or exclude uncommon risks.

These findings apply to this completed phase 3 trial, its study population, interventions, outcome definitions and reported analysis. The registry record does not report a minimal clinically important difference for the pain scale, the original sample-size justification, or detailed missing-data sensitivity analyses. Consequently, the estimates should be read as evidence about the reported comparison with stated uncertainty, not as universal proof of benefit, harm, equivalence or absence of effect.

18. Why This Trial Matters Statistically

This trial is statistically informative because it uses random assignment to compare a patient-reported pain outcome between lorecivivint and a vehicle injection. Randomization is intended to make the groups comparable in expectation, allowing the between-group contrast to address the comparative question more directly than a before-and-after change in one group. The central estimate is therefore the difference in change, not simply the amount of change observed in either arm.

The primary result also illustrates why an estimate, confidence interval and p-value should be considered together. The point estimate is close to zero, the interval covers zero, and the p-value does not indicate a clear separation under the sponsor’s model. The interval makes the remaining uncertainty visible: the result does not establish a precise effect of exactly zero, and it does not establish equivalence. These distinctions are central to interpreting clinical trial evidence responsibly.

The contrast between the sponsor’s mixed-model result and the unadjusted recalculation is another useful statistical lesson. A summary-statistic calculation can serve as a transparent check, but it is not a substitute for the analysis performed on trial data using the stated model. Differences in method may lead to slightly different inferential summaries. The model’s details are not reported in the registry record, so the sponsor result can be described but not fully reconstructed from the record.

Finally, multiple outcomes and follow-up times make the secondary findings harder to interpret than a single isolated p-value suggests. The registry lists several secondary outcomes, and the strategy for controlling multiplicity is not reported. Planning illustrations likewise should not be confused with observed trial performance: they show how assumptions about effect size and power translate into design sample sizes, not the trial’s probability of success. Together, these points show why statistical interpretation depends on design, analysis, uncertainty and reporting—not on a single number.

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 leaves several trial-specific details unavailable. It does not report the original sample-size calculation or its assumed target effect, variance, planned power or other design inputs. The planning illustrations based on the observed effect cannot fill that gap. The record also does not describe the full mixed-model specification, so the primary analysis cannot be independently reconstructed from the method label and summary results alone.

Missing-data reporting is limited. The primary analysis used observed data without imputation, but the registry record does not describe the reasons for missing observations, their distribution by group, or sensitivity analyses under alternative missingness assumptions. The analysis population also required participants to have received an injection, rather than including every randomized participant by definition. The record does not provide enough detail to assess how these choices affected the estimate.

The registry lists multiple outcomes and time points but does not report a multiplicity strategy. This limits confidence in treating isolated secondary findings as confirmatory. Numerical results are not reported in the registry record for the listed Patient Global Assessment outcomes, so those outcomes cannot be incorporated into a complete assessment of the secondary evidence.

The pain endpoint is patient-reported, and the registry defines the scale but does not provide a minimal clinically important difference. The clinical meaning of the estimated difference and of the interval therefore cannot be determined using a threshold specified in the record. Safety summaries are event counts and do not establish causation; the record’s counts also provide limited precision for comparing uncommon serious events. These limitations constrain interpretation of the registry results and do not, by themselves, demonstrate that the trial was improperly conducted.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Patient-Reported Outcomes in Evaluating Lorecivivint (SM04690) for Moderate to Severe Knee Osteoarthritis (STRIDES-1) — NCT04385303.
• Registry record last updated 2026-02-04; status last verified 2026-01.
• Results first posted 2026-02-04.
• 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

STRIDES-1 (NCT04385303) was a completed phase 3, randomized, multicenter, parallel-group study comparing a single intra-articular lorecivivint injection with vehicle in people with moderately to severely symptomatic knee osteoarthritis. The primary endpoint was change from baseline in weekly average daily target-knee pain at Week 12, measured on an 11-point Numeric Rating Scale.

The sponsor-reported mean difference was -0.07, with a 95% confidence interval from -0.46 to 0.31 and p = 0.703. The estimate is close to zero, and the interval includes zero, so the posted primary analysis does not show a clear separation between groups. This does not prove equivalence or establish the absence of any effect. Secondary estimates do not show a consistent clear separation, while numerical Patient Global Assessment results are not reported in the registry record. Details of the original sample-size justification, multiplicity strategy and missing-data sensitivity analyses are also not reported.