Study of Diclofenac Capsules to Treat Osteoarthritis Pain: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study of Diclofenac Capsules to Treat Osteoarthritis Pain (NCT01461369), a randomized phase 3 study. The primary outcome is Change From Baseline to Week 12 After Trial Entry in Osteoarthritis Pain Measured on the Western Ontario and McMaster Universities Osteoarthritis Index (WOMAC) Pain Subscale Score..

2. Clinical Question

This is a question about an average score difference between randomized groups, not about whether every participant had a similar experience. The primary measure captures pain over the last 24 hours using five visual analogue scale questions. Additional pain assessments and other WOMAC or pain measures were listed as secondary outcomes, so they provide related but separate evidence from the primary Week 12 comparison.

3. Trial Design

The registry identifies NCT01461369 as a completed Phase 3 study titled “Study of Diclofenac Capsules to Treat Osteoarthritis Pain.” Its official title describes a multicenter, randomized, double-blind, placebo-controlled, fixed-dose, parallel-group efficacy and safety study in subjects with osteoarthritis of the knee or hip. The record lists triple masking. It reports enrollment of 305, with a study start in 2011-10 and primary completion in 2012-03.

The parallel-group design assigned participants to one of two diclofenac schedules or placebo. The active schedules were diclofenac 35 mg two times daily and diclofenac 35 mg three times daily. The primary outcome analysis lists 102 participants for the two-times-daily group, 96 for the three-times-daily group, and 96 for placebo. These are the available analysis counts for that outcome, not a substitute for the enrollment figure: the registry defines the primary outcome population as subjects who received at least 1 dose and had measurements available at the specified time.

The primary endpoint was change from baseline to Week 12 or early termination in the WOMAC pain subscale. Sponsor-reported primary comparisons used a Mixed Models Analysis and reported differences in least-squares means. The registry record does not report the randomization procedure, the detailed masking procedures, the original sample-size justification, or the planned statistical analysis beyond the information in the outcome record. It also does not report the basis for the listed enrollment target. These omissions mean the design can be described from the recorded features, but the underlying protocol decisions cannot be reconstructed from the registry record alone.

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: Intent-to-Treat Population. All subjects who received at least 1 dose of trial drug and had available measurements at the time specified.

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.

6. Primary Endpoint

The registry lists the primary outcome as Change From Baseline to Week 12 After Trial Entry in Osteoarthritis Pain Measured on the Western Ontario and McMaster Universities Osteoarthritis Index (WOMAC) Pain Subscale Score., measured over Baseline to Week 12/Early Termination.

The primary endpoint was change from baseline to Week 12 after trial entry, with the timeframe also stated as baseline to Week 12 or early termination. Pain was measured with the WOMAC pain subscale. The record describes this score as the average of visual analogue scale responses to five pain questions. For each question, the participant marks a 100 mm horizontal line to indicate pain over the last 24 hours, with 0 mm representing “No Pain” and 100 mm representing “Extreme Pain.” The endpoint is expressed in millimetres.

The score difference is calculated as the Week 12 score minus the baseline score. Consequently, a negative change indicates a lower pain score at the outcome assessment than at baseline; a more negative group mean reflects a larger average decrease on this scale. This direction describes the score, not a judgment about whether an individual change is important.

General: a baseline-to-follow-up change measure uses each participant’s starting score as the reference point, which can make the result easier to interpret as change during follow-up than a follow-up score alone. The group comparison then estimates how average change differs between treatment assignment groups. The registry identifies the reported measure as a least-squares mean and its dispersion as a standard error. The record does not report a threshold for a clinically important difference, so the numerical changes alone do not establish how meaningful a particular difference would be to participants.

7. Results Posted in the Registry

• Diclofenac 35 mg Two Times Daily: mean -39.04 versus -32.46 on control; difference -6.58 (95% CI -14.68 to 1.52), standardized effect d = -0.23; z-test p = 0.111.
• Diclofenac 35 mg Three Times Daily: mean -44.14 versus -32.46 on control; difference -11.68 (95% CI -20.01 to -3.35), standardized effect d = -0.40; z-test p = 0.006.

8. Secondary Efficacy Endpoints

The registry also posts results for secondary outcomes. For each outcome below, the endpoint type, the test applied to the posted summary statistics, the result and its interpretation are given in turn. Secondary endpoints are usually not adjusted for multiple testing, so they support rather than confirm the primary finding.

Change From Baseline to Week 2 After Trial Entry in Osteoarthritis Pain Measured on the Western Ontario and McMaster Universities Osteoarthritis Index (WOMAC) Pain Subscale 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 errors.
• Result:
  • Diclofenac 35 mg Two Times Daily: mean -31.40 versus -21.60 on control; difference -9.80 (95% CI -17.46 to -2.14), standardized effect d = -0.36; z-test p = 0.012.
  • Diclofenac 35 mg Three Times Daily: mean -37.42 versus -21.60 on control; difference -15.82 (95% CI -23.71 to -7.93), standardized effect d = -0.58; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Diclofenac 35 mg Two Times Daily than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Diclofenac 35 mg Three Times Daily than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Change From Baseline to Week 6 After Trial Entry in Osteoarthritis Pain Measured on the Western Ontario and McMaster Universities Osteoarthritis Index (WOMAC) Pain Subscale 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 errors.
• Result:
  • Diclofenac 35 mg Two Times Daily: mean -36.64 versus -31.08 on control; difference -5.56 (95% CI -13.61 to 2.49), standardized effect d = -0.20; z-test p = 0.176.
  • Diclofenac 35 mg Three Times Daily: mean -43.51 versus -31.08 on control; difference -12.43 (95% CI -20.71 to -4.15), standardized effect d = -0.45; z-test p = 0.003.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Diclofenac 35 mg Two Times Daily and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Diclofenac 35 mg Three Times Daily than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Change From Baseline to the Average of Weeks 2, 6, and 12 After Trial Entry in Osteoarthritis Pain Measured on the Western Ontario and McMaster Universities Osteoarthritis Index (WOMAC) Pain Subscale 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 errors.
• Result:
  • Diclofenac 35 mg Two Times Daily: mean -35.62 versus -28.14 on control; difference -7.48 (95% CI -14.80 to -0.16), standardized effect d = -0.28; z-test p = 0.045.
  • Diclofenac 35 mg Three Times Daily: mean -41.38 versus -28.14 on control; difference -13.24 (95% CI -20.79 to -5.69), standardized effect d = -0.49; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Diclofenac 35 mg Two Times Daily than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Diclofenac 35 mg Three Times Daily than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes follow a broadly related pattern: the posted comparisons generally point toward more negative WOMAC pain changes for diclofenac than placebo, with the pattern more consistent for the three-times-daily schedule than for the two-times-daily schedule. The secondary set includes pain assessed at Week 2 and Week 6, an average across Weeks 2, 6, and 12, a composite WOMAC measure covering pain, stiffness, and function, and pain intensity measured with a visual analogue scale. These outcomes extend the primary pain question across assessments and related measures, but they are not interchangeable endpoints.

At the level of the registry’s reported analyses, the secondary findings are consistent in direction with the primary result, while the strength of evidence varies by schedule and assessment. They can help show whether the primary pattern appears at other time points or in related measures. They do not independently settle the primary question, and they do not establish that every measure has the same interpretation or precision. The individual secondary estimates and analyses should be read on their own terms.

Unadjusted secondary results carry less weight when several outcomes or time points are examined. General: making multiple comparisons increases the chance that at least one result appears notable by chance, even if there is no corresponding underlying difference. A prespecified multiplicity strategy can address that issue, but the strategy for these secondary analyses is not reported in the registry record. Accordingly, the secondary results are best treated as supportive context rather than as a collection of independent confirmatory findings. Their relation to the primary result is informative, but the registry record does not establish that they were protected against the consequences of multiple testing.

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

• Change From Baseline to Week 2 After Trial Entry in Osteoarthritis Pain Measured on the Western Ontario and McMaster Universities Osteoarthritis Index (WOMAC) Pain Subscale Score.
• Change From Baseline to Week 6 After Trial Entry in Osteoarthritis Pain Measured on the Western Ontario and McMaster Universities Osteoarthritis Index (WOMAC) Pain Subscale Score.
• Change From Baseline to the Average of Weeks 2, 6, and 12 After Trial Entry in Osteoarthritis Pain Measured on the Western Ontario and McMaster Universities Osteoarthritis Index (WOMAC) Pain Subscale Score.
• Change From Baseline to the Average of Weeks 2, 6, and 12 After Trial Entry in Osteoarthritis Pain, Stiffness, and Function Measured Using the Total (Composite) Western Ontario and McMaster Universities Osteoarthritis Index (WOMAC) Score.
• Change From Baseline to the Average of Weeks 2, 6, and 12 After Trial Entry in Pain Intensity Difference Measured Using the 100-mm Visual Analogue Scale.

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is a continuous measure, so it is summarized as a mean score change for each group and as a difference between group means. The registry lists least-squares means and standard errors for the primary outcome. It also reports the sponsor’s comparison as a difference in least-squares means from a Mixed Models Analysis. Least-squares means are model-based group averages; they need not be identical to simple arithmetic averages, particularly when a model accounts for features of the data. The registry does not provide enough detail to identify all model terms or assumptions.

What does the mean difference describe?

The mean difference is calculated as the active-treatment group’s change minus the placebo group’s change. A negative estimate means that the active group’s mean change was more negative than the placebo group’s mean change. Since lower WOMAC pain scores represent less pain on the described scale, the direction indicates a greater average reduction in score relative to placebo. The estimate is a contrast between group averages; it does not tell how many individuals improved or how their responses varied.

The posted recalculations are labeled unadjusted and are simple comparisons derived from the outcome summaries. The standard deviations used in those recalculations are approximate, as identified in the record. These calculations do not reproduce the sponsor’s Mixed Models Analysis. In particular, the recalculated confidence intervals and p-values differ from the sponsor-reported values. Because a discrepancy is recorded, the sponsor’s own analysis takes precedence when describing the trial’s primary inferential result.

How should a confidence interval be read?

A confidence interval gives a range of estimates compatible with the data and the analysis procedure, subject to its assumptions. For the primary comparisons, the sponsor reports 95% confidence intervals. An interval that includes zero is compatible with no average difference under that analysis; it can also include nonzero differences. An interval entirely below zero indicates that the estimates covered by that interval are in the direction of a more negative change in the active group. The interval’s width conveys precision: narrower intervals indicate more precise estimates, while wider intervals leave more uncertainty about the size of the difference.

A p-value summarizes how unusual the observed data, or more extreme data, would be under a specified null hypothesis and analysis assumptions. It is not the probability that the null hypothesis is true, and it does not quantify the size or clinical importance of an effect. The sponsor-reported p-values belong to the sponsor’s model-based analyses; the recalculated unadjusted p-values are a different analysis. They should not be treated as interchangeable.

Why can over-dispersion matter?

General: over-dispersion occurs when observed variability is greater than a statistical model expects. If a model understates variability, standard errors can be too small and confidence intervals too narrow; if variability is appropriately represented, uncertainty estimates are more credible. This concept is especially relevant to outcomes whose variation may not match a simple model’s assumptions. The primary outcome is continuous, and the registry identifies standard errors for its least-squares means, but it does not report a specific over-dispersion assessment or a reason to apply one. No such procedure should be inferred from the posted record.

What can the design information establish?

Randomization supports a comparison of assigned groups by reducing systematic differences at allocation in expectation. Placebo control supplies a concurrent reference group, while the parallel-group structure means the listed groups are followed as separate assignments. These are general design principles, not evidence that every potential source of bias was eliminated in this trial. The record does not report details of sequence generation, allocation concealment, adherence, or the full analysis model. Triple masking is listed, but the record does not specify who was masked or how masking was maintained.

The primary outcome population is described as subjects who received at least 1 dose of trial drug and had measurements available at the specified time. This definition identifies a treatment-exposed population with available outcome measurements; it does not establish that all randomized participants were included in every outcome analysis. The registry does not report a complete account of missing outcomes or the assumptions used to address them. Such details matter because estimates can depend on how missing measurements are handled.

11. Confidence Intervals and Precision

The sponsor-reported 95% confidence interval for the two-times-daily comparison extends from -13.94 to 0.78 mm around a difference in least-squares means of -6.58 mm. Because zero is within this interval, the posted analysis leaves uncertainty about whether the average group difference is below zero or could be near zero or slightly above it. The interval also shows that the estimate is not precise enough to isolate a narrow range of possible differences.

For the three-times-daily comparison, the sponsor-reported difference was -11.68 mm, with a 95% confidence interval from -19.17 to -4.19 mm. This interval lies below zero, so the range of values compatible with the reported analysis is in the direction of a more negative average change for diclofenac than for placebo. It still spans a range of possible magnitudes: the point estimate is not the only value consistent with the analysis.

General: confidence intervals describe uncertainty in an estimated group contrast, not the distribution of individual participant responses. Their interpretation depends on the method and assumptions used to calculate them. Here, the intervals cited are from the sponsor’s reported Mixed Models Analysis, which takes precedence over the unadjusted recalculations because the registry record identifies a discrepancy. The recalculated intervals differ, so mixing the estimate from one analysis with the uncertainty interval from the other would be misleading.

Neither confidence interval establishes clinical importance. The record does not report a threshold for a clinically important WOMAC pain difference. Nor do the intervals account for the full set of primary and secondary questions unless an appropriate multiplicity method is applied; that method is not reported in the registry record. Precision should therefore be read as uncertainty around these specified group comparisons, rather than as a complete measure of certainty across the study.

12. Planning a Similar Trial: Sample Size

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

The planning figures are participants per arm for each two-group comparison. They are not total trial enrollment figures and do not represent observed group sizes. The planning assumptions listed for these illustrations are a two-sided significance level of 0.05, equal allocation between the two arms, a normal approximation, and an effect to detect set to the stated fraction of the observed effect. The original trial’s own sample-size assumptions and justification are not reported in the registry record.

The 80% power column describes the estimated participants per arm for a planning scenario with an 80% chance of detecting the specified effect under the stated assumptions, if that effect and model assumptions were correct. The 90% power column gives the corresponding planning count for a 90% chance. These are prospective planning quantities, not evidence that a completed analysis had either probability of finding a result. This is not observed power.

Each planning row scales the target effect relative to the observed effect: 100%, 75%, or 50%. A smaller target difference is harder to distinguish from random variation, so the planning illustration requires more participants per arm. For example, the 50% row uses a smaller effect than the 100% row and consequently gives larger per-arm requirements. The estimates are specific to each displayed comparison and outcome; they should not be treated as a universal sample-size recommendation.

These figures also do not reproduce the design of the completed study. They are calculations based on observed effects and the listed assumptions. The trial’s original planning effect, intended power, allowances for missing measurements, and other design considerations are not reported in the registry record. For time-to-event outcomes, the general convention would be to report total events, but the outcomes described in these planning illustrations are continuous; their figures are participants per arm.

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 = -6.580; pooled standard deviation σ = 29.068.
2. n = 2 × (1.96 + 0.842)² × 29.068² / -6.580² = 306.3, rounded up to 307 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 <- -6.58                      # observed difference in means
sigma <- 29.0678018824181                     # 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(1461369)
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 = 307 (80% power), 411 (90% power)
 75% of observed effect: n per arm = 545 (80% power), 730 (90% power)
 50% of observed effect: n per arm = 1,226 (80% power), 1,641 (90% power)
power.t.test: 307.3 
Simulated power at n = 307 per arm: 0.797 (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 sponsor analyses for both primary comparisons using a Mixed Models Analysis. For diclofenac 35 mg two times daily versus placebo, the sponsor reports a difference in least-squares means of -6.58 mm, a 95% confidence interval from -13.94 to 0.78, and p = 0.080. For diclofenac 35 mg three times daily versus placebo, it reports -11.68 mm, a 95% confidence interval from -19.17 to -4.19, and p = 0.002.

The separately posted recalculations are simple unadjusted re-calculations from the outcome summaries, not attempts to reproduce the mixed-model analysis. For the two-times-daily comparison, the recalculated interval is -14.68 to 1.517 and the p-value is 0.111; for the three-times-daily comparison, the interval is -20.01 to -3.353 and the p-value is 0.006. The point estimates match the sponsor’s reported values, but the confidence limits and p-values do not.

Because the registry record flags a discrepancy, the sponsor’s own analysis takes precedence for the trial’s reported inferential findings. The recalculation is useful as a transparent, unadjusted check based on posted summary statistics, but it is not the primary analysis and should not replace the sponsor’s model-based result. The record does not explain the source of the discrepancy in enough detail to resolve it independently.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists a primary Week 12 WOMAC pain endpoint and multiple secondary outcomes covering pain at different times, an averaged pain measure, a WOMAC composite measure, and visual analogue scale pain intensity. It also reports multiple comparisons between active treatment groups and placebo. When a study tests several outcomes or contrasts, the chance of at least one apparently notable result can increase. Statistical methods may control that issue by prespecifying how tests will be grouped or adjusted.

The multiplicity strategy is not reported in the registry record. It is therefore not possible to determine whether the posted p-values were adjusted, which outcomes were considered confirmatory, or how the analysis treated the family of secondary outcomes. The unadjusted recalculations should not be interpreted as multiplicity-adjusted evidence. The sponsor-reported analyses are the registry’s reported results, but the record does not state an adjustment procedure for the comparisons.

The primary outcome population is defined as the Intent-to-Treat Population consisting of subjects who received at least 1 dose and had measurements available at the specified time. That wording does not describe a conventional all-randomized analysis, because it specifies receipt of at least 1 dose and availability of the outcome measurement. The registry does not provide enough information to identify how many randomized participants lacked a measurement at each time, why data were missing, or how missing observations were handled in the mixed model.

The missing-data assumptions and sensitivity analyses are not reported in the registry record. This matters because estimates can be affected if missingness is related to outcomes or differs between groups. The record also does not report details of any interim analyses, a prespecified testing hierarchy, or a full statistical analysis plan. None of these features should be inferred from the trial’s design label or from the p-values alone.

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 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: alanine aminotransferase increased (1.0%), aspartate aminotransferase increased (1.0%), deep vein thrombosis (1.0%), malignant melanoma (1.0%), non-cardiac chest pain (1.0%).

The registry reports serious adverse events for participants at risk in each group. Serious events affected 3 of 104 participants in the diclofenac 35 mg two-times-daily group, 4 of 98 in the three-times-daily group, and 2 of 103 in the placebo group. The listed counts describe participants with serious adverse events, not the total number of event episodes. The registry also lists six serious-event terms with a reported percentage of 1.0% for each: alanine aminotransferase increased, aspartate aminotransferase increased, deep vein thrombosis, malignant melanoma, non-cardiac chest pain, and pulmonary embolism.

Other adverse events affected 11 of 104 participants in the two-times-daily group, 21 of 98 in the three-times-daily group, and 13 of 103 in the placebo group. These figures are descriptive counts from the registry record; they do not by themselves establish whether events were caused by treatment or whether groups differed reliably. The record lists deaths as null rather than giving a count, so deaths are not reported in the registry record. The serious-event figures should be read with the group denominators and the limits of the posted safety information in mind; the registry record does not provide a full event-level account in this summary.

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

The posted primary findings describe average change in WOMAC pain score, not a guaranteed response for an individual. Both active groups and placebo had negative mean changes from baseline. The sponsor-reported comparison for the two-times-daily schedule has a confidence interval that includes zero, while the sponsor-reported interval for the three-times-daily schedule lies below zero. These findings describe the trial’s group-level comparisons under the reported analysis and do not establish how any particular participant’s pain changed.

The numerical differences also do not, on their own, establish clinical importance. The registry record does not report a threshold for a clinically important change in WOMAC pain score. Statistical evidence about a group difference and evidence about the size of a difference that matters to patients are related but distinct questions. The confidence intervals communicate uncertainty about the average contrast; they do not describe the range of individual outcomes.

The study record identifies a randomized, masked, placebo-controlled design, but those design features do not eliminate every possible source of bias or uncertainty. Details about allocation procedures, adherence, missing data, and multiplicity are not reported in the registry record. The sponsor analysis takes precedence over the simple unadjusted recalculations because the registry record flags a discrepancy; even so, the record does not provide enough detail to independently resolve the differences between analyses.

The secondary outcomes offer related context, but multiple endpoints and time points raise questions about multiplicity, and the adjustment strategy is not reported. Safety counts are also descriptive and do not alone establish causation or comparative risk. Overall, the result should be understood as an estimate of average score change in the studied groups, with uncertainty and reporting limitations, rather than as a universal conclusion about treatment response or safety.

18. Why This Trial Matters Statistically

This trial illustrates why a treatment comparison should focus on the between-group contrast rather than on change within an active group alone. A negative mean change occurred in the placebo group as well as in both diclofenac groups. The primary statistical question is whether average change differed between each active schedule and placebo, and by how much. Comparing group changes makes the randomized contrast central to interpretation.

It also illustrates the practical role of confidence intervals. The sponsor’s two primary intervals do not tell the same story about their compatibility with zero: the interval for one schedule includes zero, while the other lies below zero. Looking at interval location and width gives more context than treating a p-value as a complete description. The estimates remain group averages, and the record does not provide a clinical-importance threshold for translating their size into patient-level meaning.

A further statistical issue is the distinction between a model-based sponsor analysis and a simple recalculation from posted summaries. They produce matching point estimates but different uncertainty limits and p-values. Recognizing the discrepancy prevents the unadjusted calculation from being mistaken for the trial’s primary analysis. The registry record does not give enough information to reconstruct the model fully, so the sponsor’s reported analysis is the relevant source for the trial’s inferential results.

Finally, the collection of secondary outcomes emphasizes that consistent directions across related measures can be informative without removing concerns about multiple testing. The record’s missing details on multiplicity and missing-data handling also show why registry results need to be read with attention to what is and is not documented. These are general statistical lessons drawn from the features and reporting limits of this study.

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 does not report a clinically important difference threshold for the WOMAC pain scale. That limits interpretation of the size of the posted mean differences in terms of practical importance. The primary endpoint is defined clearly enough to understand its direction and units, but the record does not provide a threshold that would distinguish a meaningful change from a smaller one.

The record identifies a discrepancy between the simple unadjusted recalculations and sponsor analyses. Although the point estimates match for the primary comparisons, the confidence limits and p-values differ. The sponsor-reported analyses take precedence, but the registry information does not explain the source of the discrepancy or allow an independent reconstruction of the mixed-model analysis.

Important analysis details are not reported in the registry record, including the original sample-size justification, full model specification, missing-data assumptions and sensitivity analyses, and multiplicity strategy. The outcome population requires at least 1 dose and an available measurement at the specified time; the record does not provide a full account of missing measurements or participants excluded from each analysis. Without those details, the robustness of the estimates to alternative analytic choices cannot be assessed from this record alone.

The safety summary provides affected-participant counts and selected serious-event terms, but deaths are not reported in the registry record and the summary does not give a full account of event timing, duration, or causal assessment. The trial’s listed enrollment should not be confused with the outcome-specific analysis counts. These limitations concern what the registry record documents; they do not establish that additional information was absent from other study materials.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Study of Diclofenac Capsules to Treat Osteoarthritis Pain — NCT01461369.
• Registry record last updated 2014-05-26; status last verified 2014-04.
• Results first posted 2014-05-26.
• 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

NCT01461369 is a completed randomized Phase 3, triple-masked, parallel-group, placebo-controlled study of diclofenac capsules for osteoarthritis pain of the knee or hip. The active schedules were 35 mg two times daily and 35 mg three times daily. Enrollment was 305.

The primary endpoint was change from baseline to Week 12 or early termination in WOMAC pain subscale score, measured in millimetres. The sponsor reported a Mixed Models Analysis for each active schedule versus placebo. The registry record flags a discrepancy with simple unadjusted recalculations, so the sponsor’s reported analyses take precedence. The record does not report the original sample-size justification, multiplicity strategy, or detailed missing-data assumptions.