Safety and Efficacy of Botulinum Toxin A Injection in Patients With Painful Artificial Knee Arthroplasty (TKA): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Safety and Efficacy of Botulinum Toxin A Injection in Patients With Painful Artificial Knee Arthroplasty (TKA) (NCT00403273), a randomized phase 2 study. The primary outcome is Participants With Clinically Meaningful Improvement in Pain Severity (0-10 cm; Higher Score on Pain Scale is Worse).

2. Clinical Question

The clinical context described in the registry is persistent pain after knee replacement when revision surgery may not be feasible, acceptable, or as successful as the initial operation. The study therefore evaluated an injection-based approach against saline, with pain improvement as its primary outcome. The primary definition required a reduction of 2 points on the pain Visual Analog Scale from baseline to follow-up. The scale ranges from 0, indicating no pain, to 10, indicating maximum pain.

The trial also recorded measures related to pain, function, stiffness, general health status, clinician assessment, muscle strength, and local joint findings. These outcomes can provide supporting context, but the primary question is specifically about the proportion meeting the stated pain-improvement threshold at the specified assessment. The registry record does not report the full rationale for selecting that threshold or the original statistical design assumptions.

3. Trial Design

The registry describes a randomized, parallel-group, phase 2 study comparing intra-articular botulinum toxin A with normal saline in people with painful total knee arthroplasty. The sponsor was Minneapolis Veterans Affairs Medical Center. The record lists enrollment as 54 and status as completed. The recorded study start is 2006-07 and primary completion is 2009-01.

Participants were assigned to a single injection of botulinum toxin A in saline or a single injection of saline alone. Both injections were placed in the painful knee arthroplasty at the screening visit. The official title describes the study as randomized, controlled, and triple-blind, while the registry masking entry says quadruple. The record does not explain the difference between those descriptions or specify which roles were masked.

The primary outcome was assessed at the 2-month post-injection visit. The primary analysis population is described as participants with follow-up data, allowing only a single total knee arthroplasty per participant. The registry results list 21 participants in the botulinum toxin group and 26 in the placebo group for this outcome. These endpoint denominators are not the same as the enrollment figure; the registry record does not provide a complete account of the reasons for missing primary follow-up data.

The investigators described a 6-month study in the brief summary, while the posted primary endpoint assessment is at 2-month follow-up. The record also lists secondary measures, including pain and function scales, a physician global assessment, a timed mobility test, muscle testing, and joint signs. Details of the randomization procedure, allocation concealment, and the original statistical analysis plan are 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.

Before assignment: No enrolled participants were excluded from analyses. Main analyses were done for Single TKA per patient, since 6 were bilateral TKAs; sensitivity analyses were done on all, regardless of unilateral or bilateral

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: all with follow-up data, allowing only single TKA per participant

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 Participants With Clinically Meaningful Improvement in Pain Severity (0-10 cm; Higher Score on Pain Scale is Worse), measured over 2-month post-injection.

The primary endpoint counts participants whose pain improved by at least the stated clinically meaningful amount: a 2-point reduction on the pain Visual Analog Scale from baseline to the 2-month follow-up. The scale runs from 0 for no pain to 10 for maximum pain, with higher scores representing worse pain. The endpoint is binary at the participant level: each person either met the improvement criterion or did not.

A threshold-based endpoint can be easier to interpret clinically than a difference in average scale scores alone. It asks how many participants reached a prespecified degree of improvement, rather than only describing the average pain score in each group. It also makes the definition of response explicit. However, reducing a continuous pain measure to a responder count discards information about the size of changes beyond the threshold and about changes that fall short of it.

The registry defines the population for this endpoint as all participants with follow-up data, allowing only a single total knee arthroplasty per participant. This means the reported responder proportions describe participants with observed follow-up, not necessarily every randomized participant. The record does not report a method for handling missing endpoint observations or clarify whether the threshold was prespecified in the original protocol.

In the posted results, 15 of 21 participants in the botulinum toxin group and 9 of 26 in the placebo group met the criterion. The reported risk difference and its confidence interval quantify the contrast in response proportions; they do not by themselves establish how robust the finding would be in a larger study or under a different analysis plan.

7. Results Posted in the Registry

• Intra-articular Botulinum Toxin: 71.4% (15/21) versus 34.6% (9/26) on control; risk difference 36.8 percentage points (95% CI 10.2 to 63.4), risk ratio 2.06 (1.14–3.74); unadjusted two-proportion z-test p = 0.012.

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.

Mean Pain VAS (0-10)

• 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:
  • Intra-articular Botulinum Toxin: mean 4.40 versus 5.70 on control; difference -1.30 (95% CI -2.84 to 0.24), standardized effect d = -0.48; z-test p = 0.099.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Intra-articular Botulinum Toxin and the control. The interval gives the range of effects that remain compatible with the data.

Physician Global Assessment of Response to Treatment

• 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:
  • Intra-articular Botulinum Toxin: 30.0% (6/20) versus 0.0% (0/26) on control; risk difference 30.0 percentage points (95% CI 9.9 to 50.1); unadjusted two-proportion z-test p = 0.003.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Intra-articular Botulinum Toxin than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Physical Function Subscale of the WOMAC at 2-months

• 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:
  • Intra-articular Botulinum Toxin: mean 48.50 versus 59.70 on control; difference -11.20 (95% CI -20.21 to -2.19), standardized effect d = -0.70; z-test p = 0.015.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Intra-articular Botulinum Toxin than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes cover related but nonidentical aspects of pain and recovery, including pain intensity, physician assessment, and physical function, as well as stiffness, mobility, general health status, strength, and joint signs. Taken together, the posted results include some measures that favor the botulinum toxin group and a pain-intensity comparison whose interval includes no difference. This is broadly compatible with a possible improvement in some reported domains, but it is not a uniformly decisive pattern across outcomes.

The secondary findings relate to the primary responder result because both pain and function can reflect patients' experience after treatment. They do not test exactly the same endpoint. The primary result asks whether participants crossed a specified pain-improvement threshold. A mean pain score describes group averages, and functional or clinician-rated measures address different dimensions. Agreement across related measures can add context, but differences among them are not necessarily contradictory.

The secondary p-values are unadjusted, and the registry lists multiple outcomes. When many comparisons are examined, apparently favorable results may arise by chance even if no underlying effects exist. Without a reported multiplicity plan or prespecified hierarchy, the nominal secondary findings carry less weight than the primary result and should be interpreted as supportive or exploratory. The registry record does not state whether all secondary outcomes were analyzed as planned, or how selective reporting was prevented.

For this reason, the overall secondary pattern is more useful as a description of consistency and uncertainty than as a collection of independent confirmations. It suggests areas that may merit evaluation in a study designed to assess those outcomes, while leaving open questions about durability, measurement, missing observations, and the reproducibility of the estimates.

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

• Mean Pain VAS (0-10)
• Physician Global Assessment of Response to Treatment
• Physical Function Subscale of the WOMAC at 2-months
• WOMAC Stiffness (0-100)
• Timed Up-and-go (TUG) Test
• QOL: SF-36 Score Physical Functioning Scale, a Generic Health Status Measure
• Number of Participants With Occurrence of Joint Erythema, Warmth, Swelling or Tenderness
• Manual Muscle Strength Testing of Knee Flexion and Extension

9. Statistical Interpretation

10. Statistical Methods Explained

Several statistical ideas help interpret the reported results. The explanations below are general; the registry does not give a complete account of the trial's original analysis plan.

What does the risk difference represent?

The primary outcome is a participant count: whether a person met the pain-improvement threshold. A risk, in this setting, is the proportion of participants in a group who met that criterion. The risk difference subtracts the comparator group's proportion from the intervention group's proportion. A positive value means the observed proportion was higher in the intervention group; a negative value would mean it was lower. The posted risk difference is 0.368. This is an absolute contrast in proportions, not a relative increase.

Relative measures answer a different question. A risk ratio compares the proportions by division, while an odds ratio compares the odds of meeting the criterion. These measures can make the relative contrast look different from the absolute contrast, especially when outcomes are not rare. The registry comparison reports a risk ratio of 2.063, with a confidence interval from 1.14 to 3.736, and an odds ratio of 4.722, with a confidence interval from 1.36 to 16.39. The risk difference is often more directly interpretable as an absolute group contrast, while the relative measures describe proportional comparisons.

How should a confidence interval be read?

A confidence interval represents uncertainty around an estimated effect under the statistical method used. It is not a range that guarantees the true effect lies within its endpoints, nor does it say which values are individually likely. For the primary risk difference, the interval runs from 0.102 to 0.634. The interval is entirely positive, but its width also shows that the estimate is not very precise. The p-value of 0.012 summarizes the incompatibility of the observed result with a no-difference model under the assumptions of the test. It does not measure the probability that the treatment has no effect.

Why can responder and mean-score results differ?

The responder analysis classifies each participant using a threshold. A continuous analysis instead uses each participant's scale value and compares group averages. Thresholding can make an outcome easier to communicate, but people with changes just on opposite sides of the cutoff are classified differently even if their underlying changes are similar. Conversely, the mean can be influenced by the distribution of individual scores and may not directly convey how many people reached a meaningful improvement. The primary responder comparison and the secondary mean pain VAS comparison therefore address related but distinct questions.

What does an unadjusted p-value mean?

An unadjusted p-value is calculated for a particular comparison without correcting for the number of other outcomes or tests considered. When a study evaluates many outcomes, the chance of seeing at least one apparently favorable result can increase. This is why the primary endpoint generally has a more central role than secondary findings, and why secondary p-values need to be considered alongside the number of comparisons and any prespecified hierarchy. The registry record does not report whether the original trial analysis adjusted for multiplicity.

What are the limits of the posted comparisons?

The posted endpoint results are group summaries and contrasts. The registry does not report adjusted estimates, covariate models, sensitivity analyses, or detailed missing-data methods for the primary result. The numerical comparisons should therefore be read as the registry's posted group-level findings, not as evidence that potential imbalances or missing observations were addressed by a particular model.

For continuous outcomes, the reported means and standard deviations describe the group summaries. A mean difference expresses the intervention group's mean minus the comparator group's mean. A negative mean difference indicates a lower mean in the intervention group when calculated in that direction. Whether lower values are favorable depends on the scale's direction and interpretation. Confidence intervals help assess whether the result is compatible with a range of group differences, while the scale definition supplies the clinical meaning.

Over-dispersion is a general concern when count data vary more than a statistical model expects; if present, it can make standard errors too small and confidence intervals too narrow. The main endpoint is a binary participant outcome rather than a rate of recurrent events, and the registry does not report an over-dispersion assessment. For repeated or clustered measurements, dependence among observations can also affect uncertainty estimates. The record does not describe such modeling details.

Finally, a p-value does not describe the size or clinical importance of an effect. Effect estimates and their confidence intervals are needed for that purpose, interpreted alongside the endpoint definition and study limitations. Here, the response threshold has a stated clinical rationale in the registry description, but the full protocol rationale and original statistical plan are not reported in the registry record.

11. Confidence Intervals and Precision

The primary risk-difference estimate is 0.368, and its 95% confidence interval extends from 0.102 to 0.634. The lower endpoint is above zero, which is consistent with a higher observed response proportion in the botulinum toxin group under the reported comparison. The interval is nevertheless broad: the data are compatible with effects of notably different magnitudes. The estimate should not be treated as an exact measure of the likely effect in a wider population.

Precision depends in part on the amount of information available and on variability in the observed outcomes. The endpoint denominators were 21 in the botulinum toxin group and 26 in the placebo group. With these group sizes, the interval communicates substantial uncertainty around the point estimate. It does not account for every possible source of uncertainty, such as missing outcome data or limitations in trial conduct that the registry does not describe.

The reported risk ratio and odds ratio also have intervals, and both are wide. Relative measures can be particularly difficult to interpret when the underlying event proportions and sample sizes are limited. The absolute risk difference provides a complementary scale for understanding the contrast; none of these measures removes the uncertainty evident in the interval estimates.

Confidence intervals are not guarantees that the true effect falls inside a particular range. They describe the performance of a statistical procedure over repeated studies under its assumptions. In practical interpretation, the primary interval is more informative than the p-value alone because it shows both the direction and the range of effects compatible with the analysis. The registry record does not report whether the interval was adjusted for multiple outcomes or for any other analysis choices.

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 illustrations based on the observed effects, not the trial's own original design assumptions. For these outcomes, the values represent participants per arm, rather than total events. The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The calculations consider detecting the stated fraction of the observed effect.

The 80% power column describes the number of participants per arm that the planning calculation estimates would be needed for an 80% chance of detecting the specified effect under those assumptions. The 90% power column gives the corresponding planning estimate for a 90% chance. These are design calculations for hypothetical future studies, not a description of the probability that the completed trial produced a correct result.

For the primary binary outcome, planning for 100% of the observed effect gives 28 participants per arm for 80% power and 37 participants per arm for 90% power. Planning for 75% of the observed effect gives 51 participants per arm for 80% power and 67 participants per arm for 90% power. Planning for 50% of the observed effect gives 113 participants per arm for 80% power and 151 participants per arm for 90% power.

The pattern is important: smaller effects need more participants to detect, while targeting a higher power level also requires a larger planned sample. These estimates rely on the observed effect, which may be unstable in a small study. They should not be mistaken for the assumptions used when the original trial was designed; those assumptions are not reported in the registry record. This is 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 = 0.346; treatment proportion p₁ = 0.714; average p̄ = 0.530.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7058 = 1.3834.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6561 = 0.5522.
4. n = (1.3834 + 0.5522)² / (0.3681)² = 27.6, rounded up to 28 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 <- 0.346153846153846                          # control proportion
p1 <- 0.714285714285714                          # 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(403273)
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 = 28 (80% power), 37 (90% power)
 75% of observed effect: n per arm = 51 (80% power), 67 (90% power)
 50% of observed effect: n per arm = 113 (80% power), 151 (90% power)
power.prop.test: 27.6 
Simulated power at n = 28 per arm: 0.794 (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. Multiplicity, Missing Data and Analysis Populations

The registry lists 17 outcome measures and 7 analyses, alongside several secondary outcomes. Testing many outcomes can increase the chance of at least one nominally favorable result, even when the outcomes are related. Statistical approaches to this issue include adjusting the significance threshold, controlling a family-wise error rate, or specifying a hierarchy in which the primary outcome is tested first and secondary outcomes are interpreted conditionally. The registry record does not report whether any such approach was planned or used.

The primary outcome population is described as all participants with follow-up data, allowing only a single total knee arthroplasty per participant. This wording identifies an available-follow-up analysis rather than clearly stating that all randomized participants were included. The primary endpoint results give group denominators, but the record does not provide a complete participant flow, the reasons for missing follow-up, or the methods used to address missing outcomes.

Missingness matters because the observed participants may differ from those without follow-up. If the likelihood of missing data is related to pain or treatment experience, a complete-follow-up comparison may not represent the randomized groups as a whole. Sensitivity analyses can examine how conclusions change under different assumptions, but such analyses are not reported in the registry record.

The record also does not report an intention-to-treat analysis, a per-protocol analysis, or a detailed definition of the analysis population beyond the primary endpoint description. The original statistical analysis plan, prespecified outcome hierarchy, and any interim analyses are not reported in the registry record. Their absence from the record does not establish that these procedures were not conducted; it means their role cannot be evaluated from the posted information.

Accordingly, the primary comparison is the clearest reported statistical result, while secondary findings need cautious interpretation. Readers cannot determine from the registry record whether multiplicity adjustment, missing-data methods, or additional planned analyses altered the reported inference.

15. 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: chest pain/new diagnosis of cad (11.5%), depression (8.7%), subarachnoid hemorrhage (4.3%), atypical chest pain (4.3%), seafood allergy (4.3%).

The registry reports serious adverse events in the safety groups. In the botulinum toxin group, 3 participants were affected among 23 at risk; in the placebo group, 9 were affected among 26 at risk. These counts describe participants with serious adverse events as recorded for the groups. They do not, on their own, establish that the injection caused or prevented an event, and the record does not provide a causal attribution analysis.

The registry also lists serious-event terms with percentages: Chest pain/new diagnosis of CAD, 11.5%; Depression, 8.7%; Subarachnoid hemorrhage, 4.3%; Atypical chest pain, 4.3%; Seafood allergy, 4.3%; and Supraventricular tachycardia, 3.8%. The posted list does not identify the treatment group for each term in the summary available, so these terms should not be assigned to a group based on this information alone.

Other adverse events affected 19 participants among 23 at risk in the botulinum toxin group and 23 among 26 at risk in the placebo group. Deaths are not reported in the registry record. The safety counts are descriptive; the record does not provide enough detail about event timing, severity beyond the serious classification, relatedness, or comparative testing to support a complete safety assessment.

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

The posted primary result shows a higher observed proportion meeting the clinically meaningful pain-improvement threshold in the botulinum toxin group than in the saline group at the 2-month assessment. The estimated risk difference is positive, its confidence interval excludes zero, and the unadjusted p-value is 0.012. These findings describe the registered comparison and its statistical uncertainty; they do not establish that every participant would experience improvement or that the effect would persist.

The result does not establish long-term benefit, because the primary outcome is assessed at 2-month follow-up. It does not show that the injection can replace revision surgery or other care, and the registry record does not report a direct comparison with those options. Nor does it establish that the treatment is appropriate for any individual. The trial addresses a research question in a defined study population and cannot be used by itself to make personal treatment decisions.

The result also does not settle safety. The registry reports serious and other adverse-event counts, but the available information does not establish causation, comparative risk, or the clinical significance of each event. A full assessment would require event-level context and longer-term follow-up, neither of which is sufficiently described in the posted summary.

Finally, a statistically notable result is not automatically a precise or broadly generalizable result. The confidence interval remains wide, endpoint data are reported for participants with follow-up, and the registry does not report the missing-data methods or multiplicity plan. The study offers evidence of a favorable observed difference on its primary endpoint, while leaving uncertainty about the size, durability, and reproducibility of that difference.

17. Why This Trial Matters Statistically

This trial illustrates why a treatment comparison should be read through its endpoint definition, effect measure, and uncertainty together. The primary result is not merely a change in average pain: it is the difference between groups in the proportion meeting a stated responder threshold. That distinction matters because a clinically interpretable threshold can answer a different question from a continuous scale comparison.

It also demonstrates the value of absolute effects and confidence intervals. A p-value alone does not convey the size or precision of a result. The risk difference provides an absolute group contrast, while its interval displays how uncertain that estimate remains. Relative measures offer another perspective, but they should not replace the absolute comparison.

The trial also shows why secondary outcomes require a hierarchy of interpretation. Pain, function, mobility, and clinician assessments are related, but they are not interchangeable. Multiple unadjusted comparisons can make isolated favorable findings less persuasive. A clear prespecified analysis plan would help readers understand which outcomes were confirmatory and how missing data and multiplicity were handled; those details are not reported in the registry record.

Finally, planning calculations based on an observed effect can illustrate how future sample size changes when a smaller effect is targeted. They are not a substitute for prospective assumptions based on a justified clinically important effect. The registry record does not report the original design rationale, so the planning figures should be understood as illustrations rather than a reconstruction of the trial's design.

18. 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.

Several limitations are specific to the information posted for this trial. The primary outcome uses an available-follow-up population, and the registry record does not report the number or reasons for missing primary observations beyond the endpoint denominators. The impact of missing data therefore cannot be assessed from the posted results.

The endpoint is measured at 2-month follow-up. The registry summary describes a 6-month study, but the primary result presented is not a long-term outcome. The durability of the observed pain response is consequently not established by this primary comparison.

The record describes masking in two different ways: the official title says triple-blind, while the masking entry says quadruple. It does not explain the difference or identify which participants, clinicians, assessors, or other personnel were masked. The randomization method and allocation concealment are also not reported in the registry record.

The posted secondary comparisons are unadjusted, and no multiplicity plan is reported. There is also no detailed account of the primary analysis model, sensitivity analyses, or prespecified statistical plan. These gaps limit assessment of how robust the findings are to analytic choices.

The endpoint counts and confidence interval indicate uncertainty, and the phase 2 study is not a definitive estimate of effects across broader settings. The safety summary lacks details about event timing, attribution, and group-specific serious-event terms. These limitations do not negate the posted findings, but they constrain how confidently the results can be generalized or used to characterize the complete benefit-harm profile.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Safety and Efficacy of Botulinum Toxin A Injection in Patients With Painful Artificial Knee Arthroplasty (TKA) — NCT00403273.
• Registry record last updated 2018-05-21; status last verified 2018-04.
• Results first posted 2016-11-18.
• 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.

22. Record Summary

The registry describes a completed, randomized, parallel-group phase 2 trial of a single intra-articular botulinum toxin A injection versus saline for painful total knee arthroplasty. The primary endpoint was a 2-point or greater reduction in pain VAS from baseline to the 2-month follow-up. Among participants with endpoint data, 15 of 21 in the botulinum toxin group and 9 of 26 in the placebo group met that criterion. The reported risk difference was 0.368, with a 95% confidence interval from 0.102 to 0.634 and an unadjusted p-value of 0.012.

The registry also lists secondary pain, function, clinician-assessment, mobility, health-status, strength, and joint-sign outcomes. Serious and other adverse-event counts are posted, but the summary does not provide full event attribution or missing-data methods. The registry record does not report the original statistical plan, multiplicity handling, or design assumptions.