A Long-Term, Placebo-Controlled X-Ray Study Investigating the Safety and Efficacy of SD-6010 in Subjects With Osteoarthritis of the Knee: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Long-Term, Placebo-Controlled X-Ray Study Investigating the Safety and Efficacy of SD-6010 in Subjects With Osteoarthritis of the Knee (NCT00565812), a randomized phase 2 study. The primary outcome is Rate of Progression of Joint Space Narrowing.

2. Clinical Question

3. Trial Design

This was a Phase 2, randomized, parallel-group study comparing SD-6010 at 50 mg and 200 mg with placebo in subjects with symptomatic knee osteoarthritis. The registry describes the study as long-term and gives a two-year objective. It records triple masking and a placebo-controlled design. The official title specifies oral administration and radiographic assessment. The registry does not identify the parties included in the triple masking.

The registered enrollment was 1457. That registry figure should not be treated as the number analyzed for every outcome: the primary outcome description says that the analyzed number represents participants evaluable for that measure, and the posted group counts vary across outcomes. The registry names the full analysis set as the population for the primary outcome, defining it as all participants randomized to the study.

The primary endpoint was the rate of progression of joint-space narrowing, measured radiographically in the medial tibiofemoral compartment of the study knee from baseline up to Month 24. The registry also lists patient-reported and clinician-assessed measures, including WOMAC scores, pain assessments, global assessments, and walking-related pain, alongside other outcomes. The study is recorded as completed. Its start and primary-completion dates are listed in the registry record, but the original design rationale, planned sample-size justification, and detailed statistical analysis plan are not reported in the registry record.

The analysis below distinguishes the registry’s reported model-based comparisons from simple unadjusted recalculations based on posted summaries. Those approaches need not produce identical estimates because they can use different statistical models and analysis details. The registry does not report enough methodological detail to establish all reasons for any difference between them.

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: A total of 5077 participants were screened in the study, out of which only 1457 participants were randomized.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: FAS included all participants randomized to the study. Here, 'number of participants analyzed' (N) signifies participants evaluable for this outcome measure.

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 (FAS) included all participants randomized to the study.

6. Primary Endpoint

The registry lists the primary outcome as Rate of Progression of Joint Space Narrowing, measured over Baseline up to Month 24.

The primary endpoint was the rate of progression of joint-space narrowing (JSN), defined as narrowing in joint-space width (JSW) over the study. It was measured radiographically in the medial tibiofemoral compartment of the knee affected by osteoarthritis. The rate was expressed as a slope in mm/year over baseline to Month 24. Negative values indicate worsening osteoarthritis.

A radiographic measure addresses structural change in the joint rather than relying only on symptoms or a participant’s overall impression. A slope expresses the rate of change over the observation period, allowing the study to compare the estimated progression between randomized groups. It is not the same as a direct measure of pain, physical function, or a participant’s perceived benefit. Those domains were included among secondary outcomes.

The posted primary group estimates were -0.101 for SD-6010 50 mg, -0.125 for SD-6010 200 mg, and -0.109 for placebo. The registry’s reported comparisons use differences in slopes from mixed models. Their confidence intervals span zero for both active-dose comparisons, so the posted estimates do not establish a clear between-group difference in the primary measure. The endpoint’s radiographic focus and its interpretation as a slope should be kept in view when considering other clinical outcomes.

7. Results Posted in the Registry

• SD-0610 50 Milligram (mg): mean -0.10 versus -0.11 on control; difference 0.01 (95% CI -0.03 to 0.05), standardized effect d = 0.03; z-test p = 0.703.
• SD-0610 200 mg: mean -0.12 versus -0.11 on control; difference -0.02 (95% CI -0.05 to 0.02), standardized effect d = -0.06; z-test p = 0.402.

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.

Patient Global Impression of Change Score

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • SD-0610 50 Milligram (mg): mean 2.97 versus 3.00 on control; difference -0.03 (95% CI -0.20 to 0.14), standardized effect d = -0.02; z-test p = 0.735.
  • SD-0610 200 mg: mean 3.02 versus 3.00 on control; difference 0.02 (95% CI -0.16 to 0.20), standardized effect d = 0.01; z-test p = 0.827.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between SD-0610 50 Milligram (mg) 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 SD-0610 200 mg and the control. The interval gives the range of effects that remain compatible with the data.

Outcome Measures in Rheumatology-Osteoarthritis Research Society International (OMERACT-OARSI) Responder Index

• 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:
  • SD-0610 50 Milligram (mg): 47.4% (222/468) versus 46.6% (219/470) on control; risk difference 0.8 percentage points (95% CI -5.5 to 7.2), risk ratio 1.02 (0.89–1.17); unadjusted two-proportion z-test p = 0.797.
  • SD-0610 200 mg: 48.2% (226/469) versus 46.6% (219/470) on control; risk difference 1.6 percentage points (95% CI -4.8 to 8.0), risk ratio 1.03 (0.90–1.18); unadjusted two-proportion z-test p = 0.625.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between SD-0610 50 Milligram (mg) 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 SD-0610 200 mg and the control. The interval gives the range of effects that remain compatible with the data.

Number of Participants With Joint Space Narrowing Progression

• 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:
  • SD-0610 50 Milligram (mg): 32.5% (136/419) versus 38.5% (165/429) on control; risk difference -6.0 percentage points (95% CI -12.4 to 0.4), risk ratio 0.84 (0.70–1.01); unadjusted two-proportion z-test p = 0.068.
  • SD-0610 200 mg: 36.2% (153/423) versus 38.5% (165/429) on control; risk difference -2.3 percentage points (95% CI -8.8 to 4.2), risk ratio 0.94 (0.79–1.12); unadjusted two-proportion z-test p = 0.489.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between SD-0610 50 Milligram (mg) 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 SD-0610 200 mg and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes address symptoms, function, global assessments, responder status, and another measure of joint-space narrowing progression. Across the posted Month 24 comparisons, the broad pattern does not show a consistent separation of either dose from placebo across the different outcome types. The secondary measures do not all assess the same construct or use the same statistical scale, so agreement or disagreement among them should not be reduced to a single overall estimate.

The primary endpoint is a continuous radiographic slope, while some secondary outcomes are continuous patient assessments and others are binary classifications. These answer related but distinct questions. A finding on a binary progression definition, for example, is not interchangeable with the estimated rate of radiographic narrowing. Secondary outcomes can add context about the range of outcomes considered, but they do not replace the primary endpoint.

The registry reports many outcome measures and analyses, and it does not report a multiplicity adjustment or a hierarchy specifying how secondary hypotheses were to be interpreted. General explanation: when many comparisons are examined, the chance of finding at least one nominally notable result by chance increases unless the analysis plan accounts for the number and structure of tests. This is why an isolated unadjusted secondary result carries less weight than a result interpreted within a prespecified testing strategy.

Secondary findings should therefore be treated as supportive or exploratory unless the registry record documents a confirmatory plan. Their overall pattern can inform whether the primary result appears consistent with other measured domains, but the current record does not provide the statistical-plan details needed to assign confirmatory status or determine how multiple testing was handled.

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

• Change From Baseline in Western Ontario and MacMaster Osteoarthritis Index (WOMAC) Composite Index Score at Month 3, 6, 12, 18 and 24
• Change From Baseline in Western Ontario and MacMaster Osteoarthritis Index Pain Subscale Score at Month 3, 6, 12, 18 and 24
• Change From Baseline in Western Ontario and MacMaster Osteoarthritis Index Pain Stiffness Subscale Score at Month 3, 6, 12, 18 and 24
• Change From Baseline in Western Ontario and MacMaster Osteoarthritis Index Physical Function Subscale Score at Month 3, 6, 12, 18 and 24
• Change From Baseline in Patient Assessment of Arthritic Pain Visual Analog Scale (VAS) Score at Month 3, 6, 12, 18 and 24
• Change From Baseline in Patient Global Assessment of Arthritic Condition Score at Month 3, 6, 12, 18 and 24
• Change From Baseline in Physician's Global Assessment of Arthritic Condition Score at Month 3, 6, 12, 18 and 24
• Change From Baseline in Pain After a 50-foot Walk Using Pain Visual Analog Scale Score at Month 3, 6, 12, 18 and 24

9. Statistical Interpretation

10. Statistical Methods Explained

What does a group mean represent?

For a continuous measure, the mean is the average value among the participants included in that outcome analysis. The primary outcome is a rate, expressed as a slope in mm/year, rather than a single joint-space measurement. The reported group means describe estimated progression within each group. A difference between group means is the quantity that directly compares an active-dose group with placebo.

For the primary endpoint, the registry reports mean slopes and standard deviations for each group. The standard deviation describes how much individual measurements vary around the group mean. It is not the same as the standard error, which describes the uncertainty in an estimated mean or contrast. A group mean can be estimated precisely even when individual observations vary, particularly when there are many evaluable participants; however, precision depends on the analysis and data, not only the spread.

What is a between-group contrast?

A contrast subtracts one group’s estimate from another’s, according to the specified order. The reported primary comparisons are differences in slopes from mixed models. The registry reports 0.012 for 50 mg versus placebo and 0.005 for 200 mg versus placebo. Because the underlying slopes are negative and negative values indicate worsening, the sign of a contrast should be interpreted using the comparison order and the endpoint definition. It should not be read in isolation as a measure of benefit.

The posted recalculations are simple, unadjusted mean differences based on the group summaries. They compare the posted treatment and placebo means without reproducing the registry’s mixed-model analysis. A model-based estimate can account for the structure and specified terms of the analysis; an unadjusted summary comparison does not necessarily do so. The registry does not report enough detail to describe all model terms or explain every difference between the methods.

How should a confidence interval be read?

General explanation: a confidence interval gives a range of values compatible with the data and the analysis under its assumptions. A narrower interval indicates greater precision, while a wider interval leaves more uncertainty about the estimate. If an interval for a difference includes zero, the data are compatible with no difference as well as with differences in either direction within that interval. This does not prove equality and does not show that every possible difference is equally plausible.

The registry’s 95% intervals for the primary mixed-model contrasts include zero. That is why the estimates do not establish a clear difference between either SD-6010 dose and placebo on the primary endpoint. The interval limits also indicate that the data do not pinpoint a single effect size. Precision and statistical significance are related but distinct: an estimate can be close to zero, and its interval can still be wide enough to include effects in both directions.

Why do the analysis methods matter?

The primary analysis is described as a mixed models analysis of differences in slopes. General explanation: mixed models can represent repeated observations or other correlated data structures, rather than treating every measurement as independent. This can be useful when measurements are collected over time from the same participant. The exact model specification, covariance structure, and missing-data assumptions are not reported in the registry record, so the analysis cannot be fully reconstructed from the reported label alone.

Some secondary outcomes are analyzed with ANCOVA or logistic regression. General explanation: ANCOVA estimates group differences while accounting for specified covariates, whereas logistic regression models the odds of a binary outcome. The registry reports an odds ratio for the logistic analyses, which is a comparison on the odds scale rather than a direct difference in the proportion of participants with an event. An odds ratio should not be treated as a risk difference.

The registry’s count and continuous summaries permit additional unadjusted comparisons, but those do not necessarily match the sponsor’s prespecified or model-based estimand. The recalculations are descriptive checks, not a replacement for the reported analysis. They also do not provide a basis for assuming that covariate adjustment, repeated-measures modeling, or other analysis choices were unnecessary.

What do p-values add?

General explanation: a p-value measures how incompatible the observed data are with a specified null hypothesis under the analysis assumptions. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of an effect. A p-value should be read together with the estimate, confidence interval, endpoint definition, and analysis plan.

The registry lists p-values for its reported analyses, but the primary interpretation is clearer when grounded in the contrast and its interval. A p-value alone cannot establish that a treatment effect is meaningful, nor can a result above a conventional threshold demonstrate that there is no effect. The registry record does not report whether or how the many analyses were accounted for in a multiplicity strategy.

Why does variability matter?

General explanation: variability among participants makes group contrasts less precise. If the outcome distribution has more variability than a statistical model assumes, standard errors and intervals can be too small unless that extra variation is accommodated. For count or binary outcomes, different modeling assumptions may be needed from those used for continuous measurements. No particular over-dispersion adjustment can be attributed to this study from the registry record; its detailed modeling choices are not reported.

11. Confidence Intervals and Precision

The primary registry estimates have 95% confidence intervals that cross zero: 0.012 with an interval from -0.023 to 0.046 for 50 mg versus placebo, and 0.005 with an interval from -0.029 to 0.040 for 200 mg versus placebo. In both comparisons, the interval includes the possibility of no difference and also values in either direction. The interval bounds describe uncertainty in the estimated contrast; they are not a range containing every participant’s outcome.

The estimates are close to zero relative to the spread of values represented by their intervals, but the intervals do not support treating the groups as identical. Rather, they leave uncertainty about the magnitude and direction of a possible difference. A non-significant result is not proof of equivalence, and an interval crossing zero does not rule out effects that may matter in a clinical context. The registry does not report an equivalence or non-inferiority framework for the primary endpoint.

The simple unadjusted recalculations also have intervals crossing zero. Their estimates and interval limits differ from the sponsor’s mixed-model results, as can occur when summary-data calculations and a fitted model are not the same analysis. The registry reports the sponsor’s model-based primary results; those should remain the principal basis for interpreting the trial endpoint.

Precision also varies across endpoints because different outcomes have different distributions, variability, and numbers of evaluable participants. The sample size enrolled is not interchangeable with the number analyzed for a particular outcome. The posted outcome-specific counts and interval widths should be considered together rather than assuming one precision level applies to every analysis.

12. Planning a Similar Trial: Sample Size

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

The sample-size figures are planning illustrations based on the observed effect, not the trial’s own original design assumptions. For the continuous and binary outcomes represented in the planning calculations, the figures are participants per arm. The stated assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The planning effect is the stated fraction of the observed effect. The record notes that time-to-event calculations, where applicable, give total events; those are not the basis for reading the primary continuous endpoint figures.

The 80% power column describes the illustrative number of participants per arm that would give an 80% chance of detecting the specified effect under those assumptions if that effect were the true one. The 90% power column uses a higher target chance of detecting it, and therefore generally requires more participants per arm. These are design calculations, not observed power.

Rows planning for 75% or 50% of the observed effect represent smaller target effects than planning for 100% of the observed effect. Smaller effects are harder to distinguish from random variation, so they require more participants per arm under the stated assumptions. Large planning figures based on a small observed effect should not be read as proof that the trial was inadequately designed: the registry’s original sample-size justification and assumptions are not reported in the registry record.

These illustrations simplify the design problem. They do not incorporate every possible feature of the trial, such as the precise mixed-model specification, missing-data assumptions, or any multiplicity strategy. They should be read as hypothetical planning scenarios using the stated assumptions, not as a reconstruction of the trial protocol.

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 = 0.008; pooled standard deviation σ = 0.306.
2. n = 2 × (1.96 + 0.842)² × 0.306² / 0.008² = 22,947.2, rounded up to 22,948 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 <- 0.00799999999999999                      # observed difference in means
sigma <- 0.305869262683914                     # 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(565812)
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 = 22,948 (80% power), 30,720 (90% power)
 75% of observed effect: n per arm = 40,795 (80% power), 54,613 (90% power)
 50% of observed effect: n per arm = 91,789 (80% power), 122,880 (90% power)
power.t.test: 22948.1 
Simulated power at n = 22,948 per arm: 0.798 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The sponsor’s own primary analysis is the registry-reported mixed models analysis of difference in slopes. It reports a 50 mg versus placebo difference of 0.012 with a 95% confidence interval from -0.023 to 0.046, and a 200 mg versus placebo difference of 0.005 with an interval from -0.029 to 0.040. The intervals include zero in both comparisons.

The posted recalculations use unadjusted comparisons derived from group summary statistics. They give estimates of 0.008 for 50 mg and -0.016 for 200 mg, with both intervals also including zero. These recalculations are not the same analysis as the sponsor’s model-based contrasts and should be treated as supplementary checks rather than replacements.

The registry does not report enough detail to fully reconcile the exact differences in estimates, including all model specifications and analysis decisions. The sponsor’s reported analysis is the primary analysis to use when describing the trial’s own result. The recalculations can help readers see how summary means compare, but they do not supersede the registry’s reported statistical method.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists 44 outcome measures and 252 analyses. It also lists a range of secondary clinical measures at several follow-up times. The statistical plan describing how these outcomes and comparisons were prioritized, and whether any multiplicity correction was used, is not reported in the registry record. No interim analyses are reported in the registry record.

General explanation: multiplicity arises when several hypotheses are tested. If each test is judged separately without an adjustment or a prespecified hierarchy, the chance of at least one apparently notable result can rise. Possible approaches include adjusting significance thresholds or specifying a sequence of tests, but the registry record does not establish that either approach was used in this trial. Consequently, a single secondary p-value should not be treated as though it arose from one isolated, prespecified test.

The primary population is described as the full analysis set, including all randomized participants, but the registry clarifies that the number analyzed for the endpoint means those evaluable for that outcome. This distinction means the randomized population and the analyzed group counts need not be identical for each measure. The exact reasons for outcome-specific differences in evaluable numbers are not reported in the registry record.

The missing-data methods, assumptions, and sensitivity analyses are not reported in the registry record. That limits assessment of whether missing outcomes could have affected the estimates or their uncertainty. The record also does not report a complete statistical analysis plan or the original sample-size justification. These omissions do not show that a particular method was or was not used; they mean the registry record does not permit that conclusion.

16. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: osteoarthritis (1.4%), chest pain (0.8%), atrial fibrillation (0.6%), myocardial infarction (0.6%), arthralgia (0.6%).

The registry reports serious adverse event counts by treatment group, with participants at risk and participants affected. For SD-6010 50 mg, 43 participants were affected among 482 at risk; for SD-6010 200 mg, 61 were affected among 485 at risk; and for placebo, 49 were affected among 485 at risk. These are counts of participants with serious adverse events, not counts of every event occurrence.

The most frequently listed serious adverse event terms include osteoarthritis (1.4%), chest pain (0.8%), atrial fibrillation (0.6%), myocardial infarction (0.6%), arthralgia (0.6%), and cystocele (0.6%). The registry’s figures should be read as posted and do not by themselves establish whether a particular event was caused by treatment. The record does not report deaths in the posted serious-event data; deaths are not reported in the registry record.

Safety comparisons require attention to the event definitions, observation period, exposure, and analysis methods. Those details are not all specified in the registry record. The counts alone do not support a causal conclusion or a complete characterization of safety.

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

The primary finding is an estimated difference in radiographic joint-space narrowing slopes between each SD-6010 dose and placebo. The registry’s mixed-model confidence intervals include zero for both dose comparisons. The posted data therefore do not establish a clear difference on the primary endpoint, while still leaving uncertainty about the size and direction of any possible difference.

This is not proof that the treatments and placebo are equivalent, and it is not proof that no effect exists. Establishing equivalence would require a suitable design and prespecified equivalence margins, neither of which is reported in the registry record. Likewise, the estimates do not establish that SD-6010 works or does not work. They describe the posted trial results for specified outcomes and analyses.

The radiographic endpoint concerns structural progression, not every aspect of osteoarthritis or a participant’s experience. Symptom, pain, function, and global-assessment outcomes are separate measures. A result on one endpoint cannot automatically be generalized to all those domains, and an isolated secondary result does not supersede the primary analysis without a documented testing strategy.

The posted serious adverse event counts provide descriptive safety information, but they do not establish causation. Interpretation is also limited by missing information about the analysis plan, missing data, multiplicity, and detailed event methods. Readers should distinguish what the registry directly reports from explanations that would require information not reported in the registry record.

18. Why This Trial Matters Statistically

This trial is statistically informative because it combines a randomized, placebo-controlled design with a structural endpoint measured over time. The primary measure is a radiographic slope, making the target comparison a difference in progression rates rather than a simple end-of-study group average. That choice focuses the analysis on structural change, while the secondary measures address symptoms and participant or clinician assessments.

The posted results illustrate why estimates and confidence intervals matter more than a binary reading of a p-value. Both primary model-based intervals include zero, and they also span values on either side of it. The result is uncertainty about the magnitude and direction of the between-group contrast, not confirmation of equality. The endpoint’s negative-value convention also makes it important to understand the measure before interpreting a positive or negative contrast.

The record also offers a useful distinction between model-based results and unadjusted recalculations from group summaries. Those comparisons may differ because they do not necessarily estimate the same quantity under the same assumptions. Keeping the sponsor’s reported analysis primary avoids treating a simplified recalculation as if it were the trial’s complete analysis.

Finally, the breadth of secondary analyses makes multiplicity and reporting detail important. The registry record does not report the statistical plan, missing-data methods, or multiplicity approach. Those gaps constrain how confidently secondary results can be used to reinforce or challenge the primary finding. Clear interpretation depends not only on the numerical estimates, but also on knowing how analyses were planned and conducted.

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 analytical details unspecified. It does not report the original sample-size justification, a complete statistical analysis plan, the missing-data methods, or the handling of multiplicity. The model label for the primary analysis is reported, but the full model specification and assumptions are not. These gaps make it difficult to reconstruct the sponsor’s analysis or assess how sensitive it may be to analytic choices.

The outcome-specific numbers analyzed differ, and the registry defines the primary analysis population as all randomized participants while also defining the analyzed number as those evaluable for the outcome. Reasons for non-evaluability and the handling of missing measurements are not reported in the registry record. This limits assessment of possible selection or missing-data effects.

The primary endpoint is a radiographic measure of structural progression. It does not, by itself, capture pain, daily function, or overall participant experience. The listed secondary measures address some of those domains, but the breadth of outcomes and analyses makes their interpretation dependent on an unreported multiplicity strategy. Secondary findings should not be treated as definitive merely because one comparison is nominally notable.

Safety information is also limited to the posted serious-event summaries. The registry record does not supply all details needed to assess event timing, exposure-adjusted rates, attribution, or how events were adjudicated. The record’s absence of a reported death count cannot be interpreted as evidence that no deaths occurred.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Long-Term, Placebo-Controlled X-Ray Study Investigating the Safety and Efficacy of SD-6010 in Subjects With Osteoarthritis of the Knee — NCT00565812.
• Registry record last updated 2016-12-30; status last verified 2016-11.
• Results first posted 2016-12-30.
• 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

NCT00565812 is a completed Phase 2 randomized, triple-masked, parallel-group, placebo-controlled study of SD-6010 in subjects with symptomatic knee osteoarthritis. The registered enrollment was 1457. The primary endpoint was radiographic rate of joint-space narrowing progression in the medial tibiofemoral compartment from baseline up to Month 24.

The sponsor-reported mixed-model comparisons of both SD-6010 doses with placebo have 95% confidence intervals that include zero. The result does not establish a clear difference in the primary endpoint, while leaving uncertainty about the possible effect. The registry also reports secondary clinical and safety outcomes, but does not report key details on multiplicity, missing-data methods, or the complete statistical analysis plan.