Senolytic Drugs Attenuate Osteoarthritis-Related Articular Cartilage Degeneration: A Clinical Trial: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Senolytic Drugs Attenuate Osteoarthritis-Related Articular Cartilage Degeneration: A Clinical Trial (NCT04210986), a randomized phase 1, phase 2 study. The primary outcome is Number of Participants Experiencing One or More Treatment-Emergent Adverse Event.

2. Clinical Question

The trial title refers to osteoarthritis-related cartilage degeneration, and the summary describes a safety and efficacy trial. However, the primary endpoint reported in the registry is a safety count, not a direct measure of cartilage degeneration, pain, or physical function. The listed secondary outcomes include markers associated with senescence and cartilage degeneration, as well as measures of physical performance and muscle strength. Those outcomes address biological and functional questions distinct from the primary adverse-event question.

The central statistical question for the primary endpoint is whether the observed proportions of participants with one or more treatment-emergent adverse events differ between randomized groups, and how precisely that contrast is estimated. The sponsor reports an odds ratio from a Fisher exact analysis; a separate unadjusted calculation expresses the contrast as a risk difference. These measures describe the same event data on different scales and should not be treated as interchangeable numerical estimates.

3. Trial Design

The registry describes a Phase I/II, randomized, double-blind, placebo-controlled trial with quadruple masking and a parallel-group model. The recorded enrollment is 75. The trial condition is knee osteoarthritis, and the sponsor is Steadman Philippon Research Institute. Its status is completed; the recorded start date is 2020-01-06 and the primary completion date is 2023-01-05.

Participants were assigned to fisetin or placebo. Fisetin was described as 100 mg capsules, taken orally for two consecutive days, followed by 28 days without treatment, with a second course on two consecutive days. Placebo capsules followed the same schedule. The record therefore describes a comparison intended to distinguish the outcomes associated with the active intervention from those observed under placebo, while masking was used to reduce the influence of treatment knowledge on trial conduct or assessment.

The primary endpoint population is specified as all participants randomized and dosed with study medication. The posted arm counts for this endpoint are 34 in the fisetin group and 40 in the placebo group. These endpoint counts need not be assumed to describe every aspect of recruitment, treatment exposure, or follow-up; those details are not reported in the registry record.

The trial includes secondary outcomes covering pro-inflammatory and cartilage-degeneration markers, knee physical function tests, and muscle strength. The record also posts an outcome concerning conversion to alternative treatment. The full protocol, detailed eligibility criteria, treatment adherence information, and the original rationale for the enrollment target are not reported in the registry record. The trial's own original sample-size assumptions and analysis plan are likewise 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: All participants randomized and dosed with study medication.

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: All randomized.

6. Primary Endpoint

The registry lists the primary outcome as Number of Participants Experiencing One or More Treatment-Emergent Adverse Event, measured over Duration of study, an average of 12 months.

The primary endpoint is the number of participants experiencing one or more treatment-emergent adverse events. Each participant contributes to the event count if they experienced at least one such event during the specified observation period; multiple events in one participant do not turn that participant into multiple participants for this endpoint. The registry defines the population as all participants randomized and dosed with study medication and describes the timeframe as the duration of the study, an average of 12 months.

This kind of endpoint is used to summarize whether participants experienced any treatment-emergent adverse event, rather than to measure the number, severity, duration, or clinical importance of all events. It is a broad safety summary. Two groups can have similar counts of participants with any event while differing in the types or severity of their events, so the overall count does not replace examination of serious events or event-specific details.

In this trial, 28 of 34 participants in the fisetin group and 33 of 40 participants in the placebo group experienced one or more treatment-emergent adverse events. These are observed group counts, not evidence on their own that the intervention caused or prevented an event. Interpreting the comparison also requires attention to uncertainty, the method used to compare groups, the follow-up period, and the nature of the events. The registry record does not provide a more detailed definition of what qualified as treatment-emergent for this endpoint.

7. Results Posted in the Registry

• Fisetin: 82.4% (28/34) versus 82.5% (33/40) on control; risk difference -0.1 percentage points (95% CI -17.5 to 17.3), risk ratio 1.00 (0.81–1.23); unadjusted two-proportion z-test p = 0.987.

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.

Number of Participants Who Convert to Alterative Treatment Within Each Group.

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Fisetin: 2.9% (1/34) versus 7.5% (3/40) on control; risk difference -4.6 percentage points (95% CI -14.5 to 5.4), risk ratio 0.39 (0.04–3.60); unadjusted two-proportion z-test p = 0.387.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Fisetin and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes span biological markers associated with senescence and cartilage degeneration, physical function measures for the study knee, and muscle strength. The listed function measures include walking, mobility, knee function, and stair climbing. This range means the secondary outcomes address questions that differ from the primary safety endpoint and from one another.

The registry record lists 12 posted secondary outcomes, but numerical results are not reported in the registry record for most of them. Consequently, the overall pattern across biomarker and functional outcomes cannot be characterized from the available results. In particular, the primary adverse-event result cannot be treated as evidence that cartilage markers or physical function changed in a corresponding way: safety and efficacy outcomes measure different things.

The conversion-to-alternative-treatment outcome is one secondary result with a posted comparison. The reported counts are 1 in the fisetin group and 3 in the placebo group, while the hazard ratio is 0.44 with a 95% confidence interval from 0.05 to 4.21 and p = 0.474. Its uncertainty limits what can be inferred about the timing of conversion. These data do not establish a clear secondary-outcome pattern that would alter the interpretation of the primary safety comparison.

In general, secondary results carry less weight when many outcomes or analyses are considered, unless the analysis plan specifies how multiplicity is addressed and how results should be prioritized. The record lists 47 analyses, while a multiplicity procedure is not reported in the registry record. An isolated nominal result among many assessments can arise by chance, and missing results for most secondary outcomes further restrict an overall interpretation. The primary result therefore remains a safety comparison; secondary endpoints should be understood as distinct, and any unadjusted findings treated cautiously.

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

• Change in Levels of Pro-inflammatory Markers Associated With Senescence
• Change in Levels of Cartilage Degenerating Markers Associated With OA
• Change in Physical Function of the Study Knee (6 Min Walk)
• Change in Physical Function of the Study Knee (Timed-up-and-go Test)
• Change in Physical Function of the Study Knee (Fast 4-meter Walk)
• Change in Physical Function of the Study Knee (LEK)
• Change in Physical Function of the Study Knee (Stair-Climbing Test)
• Change in Muscle Strength (Isokinetic Dynamometry)

9. Statistical Interpretation

10. Statistical Methods Explained

The primary result can be described using event counts, a risk difference, or an odds ratio. Each measure answers a related but different statistical question. Counts show how many participants in each randomized group experienced at least one event. The risk difference contrasts the event proportions on an absolute scale. The odds ratio contrasts the odds of an event between groups. Because the primary endpoint is binary for each participant, these methods treat each participant as having either experienced at least one event or not.

What does the risk difference describe?

A risk difference is the event proportion in one group minus the event proportion in the comparison group. It is an absolute contrast, expressed on the probability scale. A value of zero represents equal observed proportions. The recalculated result uses the posted group counts and is an unadjusted comparison: it does not account for other participant characteristics or use a model-based adjustment. Its confidence interval crosses zero, so the data are compatible with both a lower and a higher event proportion in the fisetin group relative to placebo.

Unadjusted recalculations from summary counts are useful for making the scale of an effect explicit, but they are not necessarily identical to the sponsor's chosen analysis. Small differences between estimates or intervals can arise because methods use different effect measures, assumptions, or calculations. The registry record reports no discrepancy flag for the primary comparison. The sponsor's reported analysis remains the trial's own posted inferential result.

Why use Fisher's exact method?

The sponsor reports a Fisher exact analysis for the primary comparison and presents its result as an odds ratio. Fisher's exact method is a test for association in a two-group binary-outcome setting. It calculates evidence against the null hypothesis using the observed arrangement of event and non-event counts, and is often useful when counts are limited. It does not require the large-sample approximation used by some other methods. The reported odds ratio is accompanied by a confidence interval, which conveys uncertainty about the magnitude and direction of the association.

An odds ratio near one corresponds to similar event odds in the groups, but its interval matters as much as its point estimate. Here, the estimate is 0.99 and the 95% interval extends from 0.25 to 4.02. Since the interval includes one and spans a broad range on either side, the result does not precisely determine the direction or size of a group contrast. The reported p-value, p > 0.9, is not the probability that the null hypothesis is true; it is a measure of how compatible the observed data are with the null model under the analysis.

How should the secondary time-to-event result be read?

The posted conversion-to-alternative-treatment result is analyzed using a log-rank method and reported as a hazard ratio. A log-rank test compares the observed timing of events between groups over follow-up, rather than treating only a single end-of-study event proportion as the outcome. A hazard ratio compares event rates over time under the assumptions of the analysis. It is not an absolute difference in the probability of converting to alternative treatment. The sponsor-reported hazard ratio is 0.44, its 95% interval is 0.05 to 4.21, and the reported p-value is 0.474. The wide interval allows substantial uncertainty about the time-to-event contrast.

In general, time-to-event methods can make use of information about when an event occurs and can account for follow-up that ends before an event, when appropriate censoring information is available. The registry record does not report the censoring details, assumptions checks, or full analysis specification for this endpoint. Therefore, interpretation should remain tied to the posted estimate and its uncertainty, not to unreported model details.

Why do wide intervals matter?

A confidence interval is a range of estimates compatible with the data and the method at the stated confidence level. In general, a wider interval indicates less precision. It does not mean that all values in the interval are equally plausible, and a 95% confidence interval is not a guarantee that the true value lies in that particular interval. Rather, the confidence level describes the long-run performance of the interval-generating procedure under its assumptions.

Binary outcomes with relatively few participants and events can yield imprecise estimates, particularly when the number of events is not large enough to tightly constrain the comparison. This general statistical issue is relevant to interpreting the primary and alternative-treatment results. A non-significant result can reflect limited information, a small underlying contrast, or both; it should not be converted into a claim of equivalence without an appropriate equivalence design and margin. The registry record does not report an equivalence margin.

Multiplicity is another general concern when many outcomes are assessed. Testing many endpoints creates more opportunities for apparently unusual results by chance, especially when results are interpreted individually without adjustment. The record lists numerous secondary outcomes and 47 analyses overall, but the statistical plan for controlling multiplicity is not reported in the registry record. Accordingly, an isolated secondary p-value, if reported, would generally warrant more caution than a single prespecified primary analysis.

11. Confidence Intervals and Precision

Precision concerns how narrowly the data locate the estimated group contrast. The primary endpoint sponsor analysis reports an odds ratio of 0.99 with a 95% confidence interval from 0.25 to 4.02. The estimate sits near one, but the interval is wide and extends on both sides of the value representing no association. It is therefore consistent with a broad range of relative odds, rather than tightly identifying the size or direction of an association.

The recalculated unadjusted risk-difference interval also includes zero. Zero on this scale represents no observed difference in event proportions. The interval's span means the primary comparison does not precisely exclude either a lower or a higher event proportion for fisetin. Because the recalculated result is a risk difference and the sponsor result is an odds ratio, their numerical values should not be compared as if they were measurements on the same scale.

Confidence intervals describe uncertainty under the analysis method; they do not indicate the probability that the true effect is within the particular interval. In general, a narrower interval provides greater precision, while a wider interval signals that the data are compatible with more possible effect sizes. Precision is not the same as clinical importance: even a precise estimate would need to be interpreted in light of the endpoint and the clinical context, which the registry record does not fully specify.

The conversion-to-alternative-treatment result is also uncertain. Its reported hazard ratio is 0.44, with a 95% confidence interval from 0.05 to 4.21. This broad range includes values on both sides of one and limits conclusions about the relative timing of conversion. The posted event counts for this outcome are 1 in the fisetin group and 3 in the placebo group; those counts are small, and the interval appropriately signals caution rather than certainty.

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 planning figures are illustrations based on the observed effect, not the trial's own original design calculations. For the binary outcomes, the entries are participants per arm. They are not total sample sizes, and they are not counts of events. If a planning analysis were for a time-to-event endpoint, the stated convention is that the figures represent the total number of events; the primary endpoint planning figures are for participants per arm.

The assumptions for these illustrations are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. The effect to be detected is specified as a fraction of the observed effect. The original trial design assumptions, including any original target effect or sample-size justification, are not reported in the registry record.

In plain language, the 80% power column gives the illustrated number of participants per arm for a design that would have an 80% chance of detecting the specified effect if that effect were true, under the listed assumptions. The 90% power column gives the corresponding number for a higher target chance of detection. These are planning concepts, not statements about the probability that the trial result is correct.

The rows that plan for 100%, 75%, and 50% of the observed effect illustrate how assumed effect size changes the required sample. A smaller effect is harder to distinguish from random variation, so detecting a smaller effect generally requires more participants. This relationship is why planning figures increase as the effect to be detected gets smaller. The observed primary comparison is imprecise, so basing a future design directly on its estimated effect may produce unstable planning values. These figures are not observed power.

13. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

n is the number of participants in each arm, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.825; treatment proportion p₁ = 0.824; average p̄ = 0.824.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5382 = 1.0549.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5382 = 0.4530.
4. n = (1.0549 + 0.4530)² / (-0.0015)² = 1,051,430.8, rounded up to 1,051,431 participants per arm for 80% power.

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

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
p0 <- 0.825                          # control proportion
p1 <- 0.823529411764706                          # treatment proportion
n_per_arm <- function(power, frac = 1) {
  q1 <- p0 + (p1 - p0) * frac               # smaller effect = fraction of the observed difference
  pbar <- (p0 + q1) / 2
  z_b <- qnorm(power)
  ceiling(round((z_a * sqrt(2 * pbar * (1 - pbar)) + z_b * sqrt(p0 * (1 - p0) + q1 * (1 - q1)))^2 / (q1 - p0)^2, 6))
}
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: n per arm = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(n_per_arm(0.80, f), big.mark = ","), format(n_per_arm(0.90, f), big.mark = ",")))

# Check against R's built-in function (unrounded n per arm)
cat("power.prop.test:", round(power.prop.test(p1 = p0, p2 = p1, power = 0.80)$n, 1), "\n")

# Simulation: how often does the z-test reject at the 80%-power sample size?
set.seed(4210986)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 1,051,431 (80% power), 1,407,568 (90% power)
 75% of observed effect: n per arm = 1,867,673 (80% power), 2,500,284 (90% power)
 50% of observed effect: n per arm = 4,198,801 (80% power), 5,621,002 (90% power)
power.prop.test: 1051431 
Simulated power at n = 1,051,431 per arm: 0.801 (20000 replicates)

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

14. Analyses Reported by the Sponsor

For the primary endpoint, the sponsor reports a Fisher exact analysis with an odds ratio of 0.99, a 95% confidence interval from 0.25 to 4.02, and p > 0.9. This is the trial's posted analysis and should be distinguished from the unadjusted recalculation based on the summary counts.

The recalculation expresses the contrast as a risk difference, while the sponsor uses an odds ratio. The two measures use different scales, so their point estimates cannot be compared directly. Both summaries indicate substantial uncertainty: the sponsor's interval includes one, and the recalculated risk-difference interval includes zero. The registry record does not flag a discrepancy for the primary result.

The sponsor's analysis is the appropriate reference for what the trial itself reported. The recalculation is supplementary and helps describe the observed contrast on an absolute scale; it does not replace the sponsor's method or establish a separate treatment conclusion. The registry record does not report additional details about covariate adjustment or a more extensive primary analysis specification beyond the method and results posted.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when a study evaluates several endpoints, time points, groups, or statistical comparisons. In general, making many separate tests increases the chance that at least one result will appear statistically unusual by chance alone. Researchers may address this through prespecified hierarchies, adjusted significance thresholds, or other strategies, but the appropriate approach depends on the design and aims.

The registry record lists 13 outcome measures, 12 posted secondary outcomes, and 47 analyses. It does not report a multiplicity adjustment, a testing hierarchy, or a detailed statistical analysis plan. It is therefore not possible to determine from the registry record whether the analyses were intended to be confirmatory or exploratory, or how the investigators planned to interpret multiple comparisons. Secondary findings should not be treated as individually definitive without that context.

Information about missing data and analysis populations is also limited. The primary endpoint describes its population as all participants randomized and dosed with study medication, but the record does not report the handling of missing endpoint observations, exclusions after randomization, or sensitivity analyses for missing data. The endpoint arm counts are posted, but they do not explain whether any observations were unavailable or how any such cases were handled.

The registry record does not report whether the primary analysis followed an intention-to-treat principle, whether participants were analyzed according to assigned group regardless of treatment received, or whether another analysis population was used. It also does not provide details on adherence, protocol deviations, or the statistical handling of withdrawals. These omissions do not establish that such procedures were absent; they mean the details are not reported in the registry record. As a result, interpretation should stay with the stated endpoint population and posted estimates without assuming additional analysis choices.

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: rotator cuff injury (2.9%), bladder perforation (2.9%), back pain (2.5%), tracheal stenosis (2.5%).

For serious adverse events, the registry reports 2 affected participants in the fisetin group, among 34 at risk, and 2 in the placebo group, among 40 at risk. It reports no deaths in either group. These are small event counts and are descriptive; they do not by themselves establish whether a serious event was caused by treatment or whether the groups have equivalent serious-event risk.

The registry also lists Rotator Cuff Injury and Bladder Perforation at 2.9% each, and Back pain and Tracheal Stenosis at 2.5% each, as leading serious-event terms. The record does not provide enough detail in the available information to attribute each listed term to a specific treatment group or to infer a treatment relationship.

Serious adverse events are distinct from the primary endpoint, which counts participants with one or more treatment-emergent adverse events of any reported seriousness. The primary counts are 28 in the fisetin group and 33 in the placebo group. Neither the broad endpoint nor the serious-event counts alone describe event duration, severity grading, relatedness, or clinical course. Those details are not reported in the registry record.

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

The posted primary data show that 28 of 34 participants in the fisetin group and 33 of 40 participants in the placebo group experienced one or more treatment-emergent adverse events. The sponsor's odds ratio is 0.99, with a 95% confidence interval from 0.25 to 4.02 and p > 0.9. The recalculated unadjusted risk-difference interval includes no difference. Together, these statistics describe an uncertain comparison, not proof that the groups have identical outcomes.

The result does not establish that fisetin prevents adverse events, causes adverse events, or has no effect on them. A high p-value is not evidence that the null hypothesis is true. The wide confidence interval permits a range of relative effects, and the available counts do not reveal event severity, attribution, or clinical significance. The serious-event counts add limited descriptive information but do not resolve these questions.

The title and summary refer to osteoarthritis and cartilage degeneration, but the primary endpoint is safety-focused. The registry lists secondary biomarker and physical-function outcomes, yet numerical results for most are not reported in the registry record. The primary safety finding therefore cannot be interpreted as evidence for or against a change in cartilage degeneration, pain, mobility, or other clinical outcomes.

The study's design was randomized and placebo-controlled, which supports a comparative framework, but interpretation still depends on outcome definitions, follow-up, missing-data handling, and analysis details. Some of those details are not reported in the registry record. The results should be read as the posted evidence from this trial, with uncertainty and scope tied to the specific endpoint and reported analyses, rather than as a broad conclusion about all possible benefits or risks.

18. Why This Trial Matters Statistically

This trial illustrates why a result should be read together with its endpoint and its precision. The primary endpoint counts participants experiencing any treatment-emergent adverse event, while the title emphasizes cartilage degeneration. Those are different questions. A safety outcome cannot substitute for a structural or functional efficacy outcome, even when both appear within the same trial.

It also illustrates the value of reporting both counts and comparative estimates. Counts describe the observed experience in each group; an odds ratio or risk difference summarizes a contrast; and a confidence interval shows how uncertain that contrast remains. A point estimate near a null value can look reassuring at first glance, but the broad interval in this case leaves substantial uncertainty. Failure to find a statistically significant difference does not show equivalence.

The trial's many secondary outcomes underline a further statistical issue: evidence across multiple measures is difficult to interpret without a prespecified analysis plan and a clear approach to multiplicity. The registry lists biological and functional domains, but most numerical secondary results are not reported in the registry record. A careful analysis therefore avoids filling the gaps with assumptions or treating a single result as representative of all outcomes.

Finally, the posted sample-size illustrations show how planning depends on the assumed effect and target power. They are based on the observed effect rather than the trial's original design rationale, which is not reported in the registry record. This distinction matters when using a completed trial to inform future research: an uncertain observed effect can produce unstable planning estimates, and a planning calculation is not a measure of what the completed study achieved.

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 important trial details unavailable. It does not report the full eligibility criteria, the original sample-size justification, or the original statistical analysis plan. It also does not provide the handling of missing data, protocol deviations, treatment adherence, or withdrawals. These limits make it difficult to assess how closely the posted analyses follow the planned design and how robust the results are to alternative assumptions.

The primary endpoint is a broad indicator of at least one treatment-emergent adverse event. The available information does not provide a full event-level account, severity grades, event durations, or attribution to study medication. The serious-event data report small counts and no deaths, but do not by themselves establish causation or permit a detailed comparison of event profiles.

Although a range of biological and functional secondary outcomes is listed, numerical results for most are not reported in the registry record. This prevents assessment of whether those outcomes were consistent with one another or with the trial's title and summary. The available conversion-to-alternative-treatment result is based on few events and has a wide confidence interval, limiting precision for that secondary question.

The record lists many analyses but does not report how multiplicity was addressed. It also does not report whether any interim analyses occurred, or provide the trial's own original design assumptions. Those details should not be guessed. The recorded primary endpoint timeframe is the duration of study, an average of 12 months, while the secondary conversion outcome specifies an 18-month monitoring period; the record does not provide further details to reconcile these observation windows.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Senolytic Drugs Attenuate Osteoarthritis-Related Articular Cartilage Degeneration: A Clinical Trial — NCT04210986.
• Registry record last updated 2024-09-19; status last verified 2024-09.
• Results first posted 2024-09-19.
• 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

NCT04210986 is a completed randomized, double-blind, placebo-controlled Phase I/II parallel-group trial of fisetin versus placebo for knee osteoarthritis. The registry records enrollment of 75 and identifies treatment-emergent adverse events as the primary endpoint, assessed over the study duration, an average of 12 months.

One or more treatment-emergent adverse events were reported for 28 of 34 participants in the fisetin group and 33 of 40 in the placebo group. The sponsor's Fisher exact analysis reported an odds ratio of 0.99, a 95% confidence interval from 0.25 to 4.02, and p > 0.9. The estimate is imprecise and does not establish equivalence.

The registry lists secondary biomarker, physical-function, and muscle-strength outcomes, but numerical results for most are not reported in the registry record. The primary result should be interpreted as a broad safety comparison, not as a direct finding about cartilage degeneration or function.