Early Treatment for Acute ACL Tear: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Early Treatment for Acute ACL Tear (NCT01692756), a randomized phase 2 study. The primary outcome is Participant Pain Assessment.

2. Clinical Question

The clinical question was whether pain assessment results differed among the injection groups during the acute period after ACL injury. The study description frames the broader research as examining safety and effectiveness of Kenalog for knee pain after ACL rupture. The posted primary analysis compares the four groups using a Kruskal-Wallis test; the record does not report a specific primary pairwise comparison as the sponsor’s analysis. Pairwise mean differences can help describe the posted group summaries, but they are recalculations rather than the sponsor’s reported analysis.

3. Trial Design

This was a randomized, double-masked, parallel Phase 2 trial, listed as completed in the registry record. The enrollment field reports 49 participants. The interventions were organized into groups described as Kenalog or placebo, Kenalog then placebo, Kenalog only, and placebo. The record describes Kenalog as a 40 mg injection and specifies injections 1–2 days after injury and again 12–14 days later for the mixed and placebo regimens. The Kenalog-only group is described as receiving two consecutive intra-articular Kenalog injections; the placebo group received two consecutive intra-articular saline placebo injections at the same time periods.

The registry record does not report the allocation ratio, the method used to generate or conceal the randomization sequence, or further operational details of masking. It also does not explain precisely how the “Kenalog or Placebo” group was assigned to its two possible regimens. Those details should not be inferred from the group label.

The primary endpoint was participant pain assessment, recorded as a mean and standard deviation over a timeframe of up to seven days. The record describes VAS assessments at the initial orthopedic consult and pre-operative assessment, usually 1–7 days after the initial consult. It notes that 4 participants overlooked completing the VAS and could not be assessed after leaving the study visit. Outcome-specific group counts are reported with the pain results and differ from the overall enrollment field.

The sponsor’s reported primary analysis was a Kruskal-Wallis test across the groups, with p = 0.33. The registry record does not report the original sample-size justification, a detailed statistical analysis plan, the planned allocation ratio, or whether interim analyses were conducted. The record also does not report a detailed definition of the analysis population.

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

Analysis population for the primary outcome, as defined in the registry: A total of 4 patients (Group 1 n:1, Group 2 n:1, Group 4 n:2) overlooked completing the VAS. This was not realized until the patients had left the study visit preventing the investigator from collecting the information.

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: One patient was lost to follow-up (Group 1). Two patients withdrew prior to receiving treatment (Group 2, Group 3). One patient did not attend first study visit and did not receive allocated intervention (Group 3).

6. Primary Endpoint

The registry lists the primary outcome as Participant Pain Assessment, measured over Up to seven days.

The primary endpoint is titled “Participant Pain Assessment.” It uses a Visual Analog Scale (VAS) questionnaire to record participants’ perceived knee pain. The scale is described as running from 0, meaning no pain, to 10, meaning the worst pain imaginable. This kind of patient-reported measure is used to capture the participant’s own experience rather than relying only on an examination or laboratory measure.

Assessments were scheduled during the initial orthopedic consultation after injury and during the pre-operative assessment, usually 1–7 days after the initial consult. The registry gives a timeframe of up to seven days. The posted arm values are negative means, but the registry record does not provide a detailed calculation definition explaining how those values were derived from the assessments. They should therefore be interpreted as the outcome values posted for this endpoint, rather than assigning an unstated scoring or change convention.

The posted outcome is continuous, and the registry reports means and standard deviations for the groups. A mean gives a group’s average value, while the standard deviation describes the spread of observations around that average. The endpoint is clinically relevant to the study question because it measures pain reported by people after acute ACL tear, but the record does not report a threshold for a clinically important difference. It also does not specify how missing assessments were handled in the analysis beyond noting the missed VAS forms.

7. Results Posted in the Registry

• Kenalog Then Placebo: mean -2.20 versus -3.90 on control; difference 1.70 (95% CI -0.51 to 3.91), standardized effect d = 0.68; z-test p = 0.131.
• Kenalog Only: mean -3.60 versus -3.90 on control; difference 0.30 (95% CI -2.18 to 2.78), standardized effect d = 0.10; z-test p = 0.813.
• Placebo: mean -4.30 versus -3.90 on control; difference -0.40 (95% CI -3.04 to 2.24), standardized effect d = -0.13; z-test p = 0.766.

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.

Efficacy of Kenalog to Alleviate Knee Pain

• 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:
  • Kenalog Then Placebo: mean 18.94 versus 37.37 on control; difference -18.43 (95% CI -30.65 to -6.21), standardized effect d = -1.26; z-test p = 0.003.
  • Kenalog Only: mean 30.56 versus 37.37 on control; difference -6.81 (95% CI -23.97 to 10.35), standardized effect d = -0.33; z-test p = 0.437.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Kenalog Then Placebo than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Kenalog Only and the control. The interval gives the range of effects that remain compatible with the data.

Synovial Interleukin-1 Receptor Antagonist (IL-1ra) Concentration

• 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:
  • Kenalog Then Placebo: mean -4,956 versus -3,352 on control; difference -1,603 (95% CI -11,126 to 7,920), standardized effect d = -0.15; z-test p = 0.741.
  • Kenalog Only: mean -7,278 versus -3,352 on control; difference -3,926 (95% CI -13,263 to 5,411), standardized effect d = -0.37; z-test p = 0.410.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Kenalog Then Placebo 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 Kenalog Only and the control. The interval gives the range of effects that remain compatible with the data.

Synovial C-terminal Peptide II (CTXII) Concentration

• 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:
  • Kenalog Then Placebo: mean 0.23 versus 0.32 on control; difference -0.09 (95% CI -0.30 to 0.12), standardized effect d = -0.37; z-test p = 0.405.
  • Kenalog Only: mean 0.19 versus 0.32 on control; difference -0.13 (95% CI -0.38 to 0.12), standardized effect d = -0.46; z-test p = 0.304.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Kenalog Then Placebo 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 Kenalog Only and the control. The interval gives the range of effects that remain compatible with the data.

The registry record lists secondary pain and synovial biomarker outcomes, including interleukin measures, CTXII, COMP, GAG, and NTX-I. The available numerical summaries show that the secondary results do not form a uniform pattern across outcomes. For the reported secondary group analyses, the Kruskal-Wallis p-values include 0.08 for knee pain, 0.15 for IL-1ra, and .003 for CTXII. Pairwise recalculations also vary in their estimates and uncertainty. Those results should be interpreted as outcome-specific rather than as a single consistent signal across all secondary measures.

The primary sponsor-reported comparison has p = 0.33, so the reported secondary findings do not change the primary analysis result. A secondary endpoint may offer context about pain or biological measures, but it does not replace the prespecified primary question. The registry record does not report whether these secondary comparisons were prespecified with a hierarchy or how they were intended to support the primary conclusion.

There are multiple secondary outcomes and comparisons. When many outcomes are examined, some may produce apparently notable results by chance, particularly when results are assessed without adjustment for multiplicity. The registry record does not report a multiplicity correction for the secondary analyses. An unadjusted secondary p-value therefore carries less confirmatory weight than a result from a prespecified analysis with an appropriate plan for multiple testing.

The registry record lists 12 secondary outcomes, while numerical outcome details for several listed measures are not reported in the registry record. The missing detail limits any assessment of whether the pattern is consistent across the full secondary outcome set. The available secondary results are useful for describing what was posted, but they should be treated as exploratory context rather than independent confirmation of the primary result.

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

• Efficacy of Kenalog to Alleviate Knee Pain
• Synovial Interleukin-1α (IL-1α) Concentration
• Synovial Interleukin-1β (IL-1β) Concentration
• Synovial Interleukin-1 Receptor Antagonist (IL-1ra) Concentration
• Synovial C-terminal Peptide II (CTXII) Concentration
• Synovial Cartilage Oligomeric Matrix Protein (COMP) Concentration
• Synovial Glycosaminoglycans (GAG) Concentration
• Synovial Type I Collagen Cross-Linked N-Telopeptide (NTX-I) Concentration

9. Statistical Interpretation

10. Statistical Methods Explained

What does the reported test assess?

The registry reports a Kruskal-Wallis analysis across the trial groups, with p = 0.33 for the primary endpoint. This is a rank-based method for comparing groups. Rather than requiring the analysis to be framed entirely through group means, it evaluates whether the observed values tend to occupy different positions in the combined ranking. It is often used when the distributional assumptions needed for a conventional mean-based comparison are uncertain. A significant result would indicate evidence of a group difference in the distributions, but would not by itself identify which groups differ or quantify a mean difference.

The reported p-value is not the probability that the treatments are identical, nor the probability that chance alone caused the data. It describes how compatible the observed data are with the test’s null hypothesis, under the assumptions of that test. A value such as p = 0.33 does not provide evidence of a statistically detectable group difference by this test, but it cannot establish that meaningful differences are absent.

What do the pairwise recalculations add?

The additional pairwise results are unadjusted recalculations from posted group means and standard deviations. They express the estimated mean difference between each comparison group and the registry’s control group, Kenalog or Placebo. The associated confidence intervals communicate uncertainty around those estimates. These are not the sponsor’s reported primary analysis, and they should not be mistaken for the result of the Kruskal-Wallis test.

A mean difference is directional: its sign depends on which group’s mean is subtracted from the other. The record identifies the comparator and supplies the estimates, but does not provide an interpretation threshold for the VAS outcome. A difference’s direction therefore should not be translated into a judgment about clinical importance without the endpoint’s scoring definition and a relevant threshold.

The pairwise p-values are unadjusted. When several comparisons are examined, the chance of at least one apparently unusual result can increase unless the analysis accounts for multiplicity. The registry record does not report an adjustment for these recalculations. They are best read as exploratory descriptions, not as a set of confirmatory tests.

What do standard deviations and confidence intervals convey?

A standard deviation describes how dispersed individual observations are around a group mean. It is not the uncertainty in the mean itself. The standard error, by contrast, describes the estimated sampling uncertainty in a mean or contrast. Confidence intervals use an estimate and its uncertainty to show a range of values reasonably compatible with the data under the calculation’s assumptions.

For the primary pairwise recalculations, each confidence interval includes zero. In general, an interval that includes zero means the data are compatible with no mean difference, as well as with values on either side of zero within the interval. The width of an interval is informative: a broad interval permits a wider range of possible effects, and a narrow interval is more precise. An interval does not assign probabilities to individual values within it, and it does not guarantee that the true value lies within the interval.

The primary outcome is continuous, and means and standard deviations are reported. The Kruskal-Wallis analysis is rank-based, while the recalculated mean differences use summary-statistic information. Those methods emphasize different features of the data. A mean-based contrast can be sensitive to skewness or outlying observations, while a rank-based test does not directly estimate a difference in means. The registry record does not report distributional diagnostics or enough individual-level information to evaluate those features independently.

Why can over-dispersion matter?

In general, over-dispersion means that observed variability is greater than a model’s assumptions allow. If a method assumes less variability than the data contain, its standard errors may be too small and its confidence intervals too narrow. That can make evidence appear more precise than it is. Conversely, modeling variability appropriately helps uncertainty estimates reflect the spread in the observations. The trial reports standard deviations, but the registry record does not report a specific over-dispersion assessment or a model-based adjustment for the primary endpoint.

The primary results should be interpreted in light of the analysis actually reported, the small outcome-specific group sizes, and the missed VAS assessments. No detailed statistical analysis plan, original sample-size justification, or interim-analysis information is reported in the registry record. The calculations based on posted summary statistics cannot recover those missing design and analysis details.

11. Confidence Intervals and Precision

Precision concerns how narrowly the data constrain an estimated effect. The primary recalculated mean differences have 95% confidence intervals that include zero: 1.7 with an interval from -0.507 to 3.907 for Kenalog Then Placebo versus Kenalog or Placebo; 0.3 with an interval from -2.181 to 2.781 for Kenalog Only versus Kenalog or Placebo; and -0.4 with an interval from -3.035 to 2.235 for Placebo versus Kenalog or Placebo. These intervals allow values on both sides of zero, so the estimated direction is not precise.

A confidence interval is a range produced by a method that, under its assumptions, would cover the underlying parameter at the stated rate across repeated applications. It is not a range containing a specified proportion of individual participants’ pain scores, and it is not a guarantee about where the true effect lies. The interval’s width is a practical indicator of uncertainty: wider intervals leave more plausible values unresolved.

The values are unadjusted recalculations from group summaries and are not the sponsor’s reported Kruskal-Wallis result. They also do not incorporate a reported multiplicity adjustment. The registry record does not report a clinically important difference for the endpoint, so the intervals cannot be classified against a registry-defined threshold for meaningful benefit or harm.

The modest group sizes and the reported missed VAS assessments are relevant to the uncertainty. The record does not describe how missing primary outcome values were handled, and it does not provide individual observations or a fuller account of the endpoint calculation. As a result, the posted intervals describe the recalculated contrasts under their calculation assumptions, not every source of uncertainty about the design, measurement, or 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 planning figures are participants per arm, not total events. The assumptions listed for these planning illustrations are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect. These calculations are planning illustrations based on the observed effect, not the trial’s original design assumptions; the original sample-size justification is not reported in the registry record.

The 80% power column gives the estimated participants per arm for a future study to have an 80% chance of detecting the specified effect under the stated assumptions, if that effect is real. The 90% power column gives the corresponding per-arm planning figure for a 90% chance. These are design targets, not guarantees about what a later study will find. The figures are not observed power.

Each comparison has rows for planning around 100%, 75%, or 50% of the observed effect. Smaller effects require more participants per arm to detect at the same power and significance level. For example, the primary comparison of Kenalog Then Placebo with Kenalog or Placebo has planning figures of 35 participants per arm for 80% power and 47 for 90% power when planning for 100% of the observed effect; the figures rise to 138 and 185 when planning for 50% of that effect. Such values are sensitive to the observed effect, which may itself be uncertain in a small trial.

The plotted planning curve should be read as a visual expression of the same relationship: as the target effect gets smaller, the required per-arm sample size increases. These illustrations do not account for design features or analysis choices that are not listed in the stated assumptions, and they should not be interpreted as a retrospective measure of the trial’s success.

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 = 1.700; pooled standard deviation σ = 2.518.
2. n = 2 × (1.96 + 0.842)² × 2.518² / 1.700² = 34.4, rounded up to 35 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 <- 1.7                      # observed difference in means
sigma <- 2.51793566240283                     # 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(1692756)
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 = 35 (80% power), 47 (90% power)
 75% of observed effect: n per arm = 62 (80% power), 82 (90% power)
 50% of observed effect: n per arm = 138 (80% power), 185 (90% power)
power.t.test: 35.4 
Simulated power at n = 35 per arm: 0.796 (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-reported primary analysis is a Kruskal-Wallis comparison of the groups, with p = 0.33. That is the trial’s own reported primary result in the registry. It tests for differences across group distributions and is not a direct estimate of a particular pairwise mean difference.

The recalculated results use the posted means and standard deviations to estimate unadjusted mean differences between the control group, Kenalog or Placebo, and each other listed group. They include confidence intervals and unadjusted p-values. Because these are based on summary statistics and answer pairwise mean-comparison questions, their results need not match the sponsor’s rank-based omnibus test. The registry record marks no discrepancy between the posted analysis and the recalculation.

The pairwise calculations are supplementary and should not be treated as a correction to, or substitute for, the sponsor’s reported analysis. They offer another way to describe the available summary data, but do not reproduce all details of the trial’s analysis. In particular, the registry record does not report a complete statistical analysis plan, a multiplicity adjustment for these recalculations, or additional methods used in the sponsor’s analysis.

Both forms of evidence should be read with the outcome-specific group sizes, missed VAS assessments, and the breadth of the confidence intervals in mind. The sponsor’s reported p-value is not proof of equivalence, and the recalculated pairwise estimates are not proof of a treatment effect. Together, they indicate that the registry record does not establish a statistically detectable primary group difference and that the pairwise mean estimates remain uncertain.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when an analysis makes several statistical comparisons or tests multiple outcomes. Even when each test uses a conventional significance threshold, repeated testing can increase the chance of at least one apparently significant result occurring by chance. This matters in a trial with multiple groups, several secondary outcomes, and possible pairwise contrasts.

The registry reports an omnibus Kruskal-Wallis p-value for the primary outcome, which addresses an overall group comparison. The unadjusted recalculations compare individual groups with the named control. The registry record does not report a multiplicity adjustment for those recalculations. It also does not report a detailed testing hierarchy or a plan specifying which secondary outcomes were confirmatory. The secondary findings, including a reported p-value of .003 for CTXII, therefore require caution and should not be treated as stand-alone confirmation.

The primary outcome record notes that 4 participants overlooked completing the VAS, and that the investigator could not collect the information after they had left the study visit. The record identifies the group allocation of those missed assessments, but does not report how missing values were handled in the analysis, whether any imputation was used, or whether a sensitivity analysis assessed the impact of missingness. It also does not report why the assessments were missed beyond the stated oversight.

The record gives outcome-specific group sizes, but does not provide a detailed analysis-population definition such as whether the primary analysis followed intention-to-treat, per-protocol, or another population. The registry record does not report the full statistical analysis plan, interim analyses, or a sample-size justification. Those omissions limit the ability to evaluate whether the reported tests and missing-data handling followed prespecified procedures. The absence of those details is not evidence that a particular method was or was not used; it means the methods are not reported in the registry record.

16. Safety Results

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

Deaths

Other (non-serious) adverse events

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

Most frequent non-serious adverse event terms

The posted safety counts distinguish serious adverse events from other adverse events and show the number at risk in each group. For serious adverse events, the record reports 0 affected in every group; the at-risk counts are 11, 11, 11, and 12, respectively. The deaths field is 0 for each group. The record lists no top serious adverse-event terms.

For other adverse events, the reported affected counts are 7 in Kenalog or Placebo, 4 in Kenalog Then Placebo, 6 in Kenalog Only, and 5 in Placebo. The corresponding at-risk counts are 11, 11, 11, and 12. These are descriptive registry counts; they do not by themselves establish that a particular regimen caused or prevented an event. The registry record does not provide event-level descriptions for these other adverse events in the registry record reported for this analysis.

Safety counts should be interpreted in light of the number at risk, the way events were collected, and the follow-up period. The record does not provide enough detail to assess event severity beyond the serious-versus-other classification, duration, or attribution. The absence of a reported serious event in these groups does not establish that serious harms are impossible.

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

The posted results describe pain assessments and other outcomes among participants in a randomized, double-masked, parallel trial of injection regimens after acute ACL tear. For the primary outcome, the sponsor-reported Kruskal-Wallis analysis has p = 0.33. The unadjusted recalculated pairwise mean differences have confidence intervals that include zero. Taken together, these results do not establish a statistically detectable primary difference among the groups or a precise direction and size for the pairwise mean contrasts.

That interpretation is narrower than saying the regimens are the same. A non-significant test does not establish equivalence, and the registry record does not describe an equivalence or non-inferiority design. The outcome-specific group sizes are limited, the primary endpoint has missed assessments, and the confidence intervals leave a range of possible mean differences unresolved. The registry record does not report a clinically important difference threshold, so the statistical estimates cannot be judged against a registry-defined clinical threshold.

The results also do not establish that Kenalog is effective or ineffective. The trial’s posted comparisons are specific to the studied groups, endpoint, and assessment period. The primary outcome is a participant-reported pain measure, while several secondary outcomes are laboratory measures. A finding in one secondary measure does not establish a corresponding change in pain or a broader clinical outcome, and the registry record does not report a full multiplicity plan for those secondary tests.

Safety counts are descriptive. The posted record reports no serious adverse events or deaths in the groups, alongside other adverse-event counts. Those figures do not prove the absence of risk, especially without additional detail on event definitions, follow-up, and attribution.

Overall, the registry record supports a cautious description: the sponsor’s primary analysis did not detect a group difference, while uncertainty remains about the possible size and direction of effects. The record does not support a conclusion of equivalence, establish clinical importance, or settle questions beyond the reported outcomes and timeframe.

18. Why This Trial Matters Statistically

This trial is statistically instructive because it places an omnibus rank-based test beside pairwise mean estimates derived from posted summary statistics. The two approaches answer related but different questions. The omnibus analysis assesses whether group distributions differ overall; a pairwise mean difference quantifies the estimated contrast between a selected group and the named control. Keeping those distinctions clear prevents a supplementary calculation from being mistaken for the trial’s reported primary analysis.

The study also illustrates why a p-value should not be read in isolation. The sponsor-reported primary p-value is 0.33, and the pairwise confidence intervals span zero and a range of values in either direction. The point estimates alone do not convey the uncertainty surrounding them. Confidence intervals and group-level variability are important for judging how precisely the registry record estimates a difference.

Multiple groups and secondary outcomes create a further interpretive challenge. An apparently notable unadjusted result among numerous analyses may arise by chance, so analysis hierarchy and multiplicity plans matter. The record does not report those details. This makes it especially important to distinguish primary evidence from secondary exploratory findings and to avoid treating a single secondary result as confirmation.

Finally, the missed VAS assessments and limited group sizes show how incomplete measurement and uncertainty are connected. Clear reporting of analysis populations, missing-data methods, endpoint definitions, and original design assumptions helps readers assess the reliability and scope of a result. Where those details are not reported, conclusions should remain tied closely to the posted estimates and their stated limitations.

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.

Several limitations specific to this trial constrain interpretation. The registry record reports 49 enrolled participants, while the outcome-specific group counts are smaller and vary across endpoints. It notes that 4 participants missed the primary VAS assessment, but does not report how those missing values were handled analytically. The effect of those missing assessments on the estimates therefore cannot be evaluated from the record.

The primary endpoint description explains the scale and assessment schedule but does not give a complete calculation definition for the negative posted means. Nor does the record report a clinically important difference threshold. These omissions make it difficult to translate the numerical contrasts into clinical importance without adding assumptions.

The sponsor’s primary analysis is an omnibus Kruskal-Wallis test, while the pairwise estimates are unadjusted recalculations from group summary statistics. They should not be conflated. The registry record does not report a full statistical analysis plan, a multiplicity strategy, an analysis-population definition, or whether interim analyses occurred. The original sample-size justification is also not reported, so the planning illustrations based on observed effects should not be treated as the trial’s design rationale.

Descriptions of the injection groups leave some operational details unclear, including how the “Kenalog or Placebo” group was assigned to the two possible regimens. The record also does not provide detailed information on event-level safety outcomes in the registry record reported for this analysis. Finally, numerical results for several listed secondary outcomes are not reported in the registry record. These gaps limit assessment of consistency across outcomes and the completeness of the safety and efficacy picture.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Early Treatment for Acute ACL Tear — NCT01692756.
• Registry record last updated 2018-12-05; status last verified 2018-11.
• Results first posted 2018-11-13.
• 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

NCT01692756 is a completed, randomized, double-masked, parallel Phase 2 trial of early anti-inflammatory treatment after acute ACL tear. The registry record reports 49 enrolled participants and compares injection regimens involving Kenalog and saline placebo.

The primary endpoint is a participant-reported VAS pain assessment over up to seven days. The sponsor-reported Kruskal-Wallis test gives p = 0.33. Recalculated unadjusted pairwise mean differences have confidence intervals that include zero; they are supplementary to, not replacements for, the sponsor’s analysis. The record notes 4 missed VAS assessments.

The registry lists 12 secondary outcomes, but numerical details for several are not reported in the registry record. No serious adverse events or deaths are reported in the listed groups. Missing-data methods, multiplicity plans, the original sample-size justification, and a detailed analysis-population definition are not reported in the registry record. The results should therefore be read as estimates with substantial uncertainty, not as evidence of equivalence.