Dose Finding Study of HP802-247 in Venous Leg Ulcers: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Dose Finding Study of HP802-247 in Venous Leg Ulcers (NCT00852995), a randomized phase 2 study. The primary outcome is The Average Percent (%) Change From Baseline in the Target Wound Area in Each Treatment Group Over the Twelve-week Double-blind Treatment Period..

2. Clinical Question

The clinical question is therefore about changes in wound area across dose and dosing-frequency groups, relative to vehicle, rather than about a single measurement at one visit. The posted primary results are group means with standard deviations. The primary analysis is described as an ANCOVA, but the registry’s own reported pairwise analyses are listed separately as two-sided t-tests. The relationship between those reported tests and the stated primary model is not fully explained in the registry record.

3. Trial Design

This was a completed Phase II, randomized, triple-masked, parallel-group study sponsored by Healthpoint. The registry lists enrollment of 228 participants and the condition as venous leg ulcer, also described as venous stasis ulcers. The study began in 2009-02, with primary completion in 2011-04. These dates and the completed status describe the trial record; they do not by themselves establish how completely outcomes were collected or reported.

Participants were assigned to one of five groups. Two groups received low-dose HP802-247, either at each visit or at alternating visits with placebo at the intervening visits. Two groups followed the same schedules at the high concentration. The fifth group received vehicle at each visit. All groups are described as receiving standard care in the brief summary. Details of the standard-care procedures, the randomization method, allocation concealment, and the masking procedures are not reported in the registry record.

The study was described as a 16-week study, while the primary outcome description specifies weekly measurement for up to 12 weeks or until wound closure, whichever occurred first. The primary endpoint timeframe is given as weekly over the 12-week treatment period, or until closure. For the secondary time-to-closure outcome, the registry notes a 14-week timeframe because the final visit for one subject was delayed by two weeks. The registry record does not explain the original sample-size justification, the assumptions used to choose enrollment, or whether any interim analyses were planned or conducted.

For the primary endpoint, the registry identifies an ITT population and defines it as subjects who received at least one dose of test article. The group counts posted for the primary outcome are 43 to 50 participants per arm. The registry does not give a fuller account of participant flow, exclusions from the analysis, or how missing weekly measurements were handled.

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: Subjects entered a 2-week run-in; subjects whose wound radius decreased by \< 0.349 cm/2weeks and met all other inclusion/exclusion (I/E) criteria were eligible for randomization.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: ITT population.: Subjects who received at least one dose of test article. The primary analysis was performed using a two-way ANCOVA model, which included treatment group (the effect of interest), site, and the baseline target wound area (the covariate), with significance being at P \< 0.05.

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 The Average Percent (%) Change From Baseline in the Target Wound Area in Each Treatment Group Over the Twelve-week Double-blind Treatment Period., measured over Weekly, over the 12 week treatment period, or until wound closure, which ever occurred first.

The primary endpoint is the average percent change from baseline in target wound area for each treatment group during the double-blind treatment period. The target ulcer was measured weekly using a laser-based wound imaging system with software to measure area. Measurement continued for up to 12 weeks or until wound closure, whichever occurred first; the registry says an average of the 12 measurements was assessed.

Wound area is a continuous measurement, so a group mean can describe the average change across participants while the standard deviation describes how variable individual measurements were within that group. Percent change puts the observed area change in relation to each participant’s baseline area. In the posted results, the group means are negative, which denotes a decrease from baseline under the stated percent-change measure. The magnitude of a group mean alone does not show how consistently participants changed, which is why the reported standard deviations and comparisons also matter.

Repeated weekly measurement can characterize the course of change during treatment rather than relying only on an endpoint visit. Averaging measurements may also represent the treatment period more broadly, although the registry record does not describe in detail how the average was formed when measurements were unavailable or when closure occurred before the final scheduled measurement. The primary analysis description specifies a two-way ANCOVA including treatment group, site, and baseline target wound area. The rationale for selecting this endpoint and the details of its operational calculation beyond the registry description are not reported in the registry record.

7. Results Posted in the Registry

• B - Low Q14D: mean -77.11 versus -60.38 on control; difference -16.73 (95% CI -27.14 to -6.32), standardized effect d = -0.64; z-test p = 0.002.
• A - Low Q7D: mean -70.15 versus -60.38 on control; difference -9.77 (95% CI -20.26 to 0.72), standardized effect d = -0.37; z-test p = 0.068.
• D - High Q14D: mean -68.14 versus -60.38 on control; difference -7.76 (95% CI -19.10 to 3.58), standardized effect d = -0.28; z-test p = 0.180.
• C - High Q7D: mean -72.89 versus -60.38 on control; difference -12.51 (95% CI -23.98 to -1.04), standardized effect d = -0.44; z-test p = 0.033.

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.

Median Time to Achieve Complete Wound Closure, Based on Based on a Kaplan-Meier Survival Analysis, Over the 12-Week Treatment Period From Baseline.

• Endpoint type: Time to event: compared as a hazard ratio.
• Test: Hazard ratio as reported by the sponsor (Regression, Cox); it was not recalculated.
• Result:
  • E - HP802-247 Vehicle vs B - Low Q14D: hazard ratio 1.83 (95% CI 1.09–3.04), reported p = 0.021 (as reported in the registry).
  • E - HP802-247 Vehicle vs A - Low Q7D: hazard ratio 1.19 (95% CI 0.69–2.05), reported p = 0.530 (as reported in the registry).
• Interpretation:
  • The 95% confidence interval excludes no difference (a ratio of 1), so the hazard of the event is statistically higher for E - HP802-247 Vehicle vs B - Low Q14D than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval includes no difference (a ratio of 1), so these data do not show a statistically significant difference between E - HP802-247 Vehicle vs A - Low Q7D and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes broaden the assessment beyond the average wound-area change. They include repeated measures of wound area, thresholds of area reduction, wound closure at visits, pain ratings, and time-to-closure measures. These outcomes capture different dimensions and time patterns, so they can complement the primary endpoint without being interchangeable with it.

The posted secondary results are incomplete relative to the outcomes listed in the registry. Time-to-closure medians and a Cox comparison are reported, but the registry does not post numerical results for every listed secondary outcome. In particular, results for the repeated visit-based measures, pain, and the proportion reaching the specified area-reduction threshold are not reported in the registry record. The absence of a posted result does not show what the unreported result would have been.

Secondary findings may support or qualify the interpretation of the primary outcome, especially when different outcome definitions point in similar or different directions. However, the registry’s multiple outcomes and analyses create opportunities for selective emphasis and chance findings. Unless the analysis plan identifies a hierarchy or adjustment strategy, unadjusted secondary p-values carry less weight than a clearly prespecified primary analysis. The registry does not report a multiplicity procedure or enough prespecification detail to determine how the secondary tests should be prioritized. Their role is therefore supportive and exploratory in interpretation, rather than a substitute for the primary endpoint.

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

• Kaplan-Meier Probability of Non-Closure
• Percent of Change From Baseline in Target Wound Area at Each of the Twelve Double-blind Treatment Weeks.
• Proportion of Subjects Achieving ≥ 50% Decrease in Target Wound Area From Baseline Through Week 13
• Percentage of Participants With Complete Wound Closure at Each Visit
• Target Ulcer Pain Was Measured Using a Visual Analog Scale [Range: 0mm - 100mm]. Subjects Marked Their Pain Level on a 100 mm Horizontal Line, With a Short Vertical Line Across the Scale, 0 Denoting no Pain and 100mm the Maximum Pain.
• Median Time to Achieve Complete Wound Closure, Based on Based on a Kaplan-Meier Survival Analysis, Over the 12-Week Treatment Period From Baseline.

9. Statistical Interpretation

10. Statistical Methods Explained

The registry describes the primary analysis as a two-way ANCOVA. ANCOVA is a regression-based method for comparing group outcomes while adjusting for specified covariates. In this trial, the stated model included treatment group as the effect of interest, site, and baseline target wound area as a covariate. Adjusting for baseline wound area can account for baseline differences in the measurement when estimating treatment-group contrasts. Including site can account for variation associated with study location. The registry states a significance criterion of P < 0.05, but details such as model diagnostics, the exact contrast procedure, and handling of missing observations are not reported in the registry record.

The primary outcome is continuous, and the posted arm summaries are means and standard deviations. A mean difference compares the average outcome in one group with the average in the vehicle group. The recalculated comparisons are unadjusted: they use posted summary statistics rather than the trial’s stated ANCOVA model. They therefore do not account for site or baseline wound area in the way the primary model is described. The recalculated intervals and p-values are useful for a transparent summary-statistic comparison, but the registry-reported analysis is the appropriate reference for the sponsor’s own inferential result.

A standard deviation describes the spread of participant-level values around a group mean. It is not the same as a standard error, which describes uncertainty in an estimated mean. Greater variability generally makes a group comparison less precise when sample sizes are otherwise similar. The posted standard deviations are substantial relative to the group means, so the average change should be read alongside the spread and the confidence intervals, not as a description of every participant’s response.

The registry also reports a secondary time-to-event outcome: median time to complete wound closure, estimated using Kaplan-Meier survival analysis. Kaplan-Meier methods account for the timing of events and can retain information from participants whose event time is not observed during follow-up by treating their follow-up as censored, subject to the method’s assumptions. The record does not give detailed censoring counts or describe the censoring assumptions. The median is the time by which the estimated event distribution reaches one-half; it is not an average time and does not convey the full shape of the event-time distribution.

For the time-to-closure comparison, a Cox regression analysis reports a hazard ratio. A hazard ratio compares the instantaneous event rates between groups over follow-up under the proportional-hazards model. Its interpretation depends on which group is in the numerator and on the event definition. The registry labels the reported comparison as vehicle versus low Q14D and provides a hazard ratio of 1.83 with a 95% confidence interval of 1.09 to 3.04 and p = .0212. The registry also reports an ANCOVA p-value for that pair, but the precise role of that ANCOVA in the time-to-event analysis is not explained. The proportional-hazards assessment and other Cox model details are not reported in the registry record.

Confidence intervals express uncertainty about an estimated effect under the model and sampling assumptions. An interval that includes the null value is compatible with no difference at the corresponding confidence level, while an interval that excludes it indicates that the data are less compatible with that null under the model. This convention does not determine clinical importance. For mean differences, the null value is zero; for a ratio measure such as a hazard ratio, the null value is one. The width of an interval reflects precision: broader intervals leave more uncertainty about the effect’s magnitude.

The posted secondary outcomes include Kaplan-Meier probability of non-closure, percent change in target wound area at each of the twelve double-blind treatment weeks, the proportion achieving at least 50% decrease in target wound area through Week 13, complete closure at each visit, pain on a 0mm to 100mm visual analog scale, and median time to complete closure. These outcomes address different aspects of the wound experience and use different statistical summaries. The registry record lists 7 outcome measures and 84 analyses, but it does not provide enough information to determine which analyses were prespecified, how repeated measurements were modeled, or whether any multiplicity adjustment was used.

For a continuous outcome, normal-based planning calculations can estimate how many participants per arm would be needed for a chosen effect under specified assumptions. For a time-to-event outcome, planning can instead be expressed in terms of total events. Such calculations are prospective illustrations; they are not measurements of the trial’s achieved statistical power. Their values depend on assumptions about the target effect, allocation, significance level, and statistical approximation. The original design assumptions and sample-size justification are not reported in the registry record.

11. Confidence Intervals and Precision

The recalculated primary comparisons include confidence intervals for the unadjusted mean differences. For low Q14D versus vehicle, the estimated difference is -16.73 with a 95% confidence interval from -27.14 to -6.318. For low Q7D, the estimate is -9.77, with an interval from -20.26 to 0.723. For high Q14D, the estimate is -7.76, with an interval from -19.1 to 3.577. For high Q7D, the estimate is -12.51, with an interval from -23.98 to -1.036. These intervals reflect uncertainty in the unadjusted comparisons calculated from the posted summaries; they are not confidence intervals from the stated ANCOVA.

The interval for low Q14D and the interval for high Q7D exclude zero, while the intervals for low Q7D and high Q14D include zero. An interval including zero does not prove that there is no difference; it indicates that the data and calculation remain compatible with zero as well as with effects in either direction. Conversely, an interval excluding zero does not establish clinical importance or account for the fact that several groups were compared. The registry-reported p-values differ from some recalculated p-values, and the sponsor’s own analysis takes precedence.

Precision also depends on variability and sample size. The primary arm counts range from 43.0 to 50.0, and the reported standard deviations range from 21.66 to 29.79. Wider intervals indicate less precision about the size of a difference. The registry does not report confidence intervals for the primary arm means themselves. For the median time-to-closure estimates, some limits are absent; those values are not reported in the registry record. The posted Cox result has a 95% confidence interval from 1.09 to 3.04, which communicates uncertainty in the hazard-ratio estimate under that model, but does not remove uncertainty about model assumptions or the broader set of comparisons.

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 illustrations translate an observed comparison into hypothetical future design sizes under stated assumptions. For the primary continuous-outcome comparisons, the figures are participants per arm, not totals across both arms. The rows consider planning for 100%, 75%, or 50% of the observed effect. Within each row, the 80% power column gives the per-arm size associated with an 80% chance of detecting the assumed effect if that effect and the calculation assumptions were correct. The 90% power column gives the corresponding size for a higher chance of detection. Smaller target effects require more participants because they are harder to distinguish from random variation.

The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation; the target effect is the stated fraction of the observed effect. For time-to-event planning, the figures are total events, not participants per arm, and use the stated Schoenfeld approach. The registry’s original design assumptions and sample-size justification are not reported in the registry record. These are planning illustrations, not observed power, and they should not be read as evidence that the completed study had a particular probability of finding a result.

Because the observed effect is used as the starting point, the calculations are sensitive to how large that observed estimate is. Observed effects can be uncertain, especially when estimated from limited samples. The planning values therefore illustrate how assumed effect size and desired power affect design requirements; they do not establish the sample size that would be appropriate for a future study without additional design decisions and assumptions.

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 = -16.730; pooled standard deviation σ = 26.330.
2. n = 2 × (1.96 + 0.842)² × 26.330² / -16.730² = 38.9, rounded up to 39 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 <- -16.73                      # observed difference in means
sigma <- 26.3297165260172                     # 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(852995)
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 = 39 (80% power), 53 (90% power)
 75% of observed effect: n per arm = 70 (80% power), 93 (90% power)
 50% of observed effect: n per arm = 156 (80% power), 209 (90% power)
power.t.test: 39.9 
Simulated power at n = 39 per arm: 0.792 (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 the sponsor’s pairwise primary analyses as two-sided t-tests against vehicle, with p-values of < 0.001 for low Q14D, 0.090 for low Q7D, 0.159 for high Q14D, and 0.029 for high Q7D. The primary analysis description elsewhere specifies a two-way ANCOVA including treatment group, site, and baseline wound area. The record does not explain how the listed t-tests relate to that stated model or whether they are the final primary inferential results.

The recalculated comparisons use unadjusted summary-statistic methods and produce p-values that differ from some sponsor-reported values. Because the registry indicates a discrepancy, the sponsor’s own analysis takes precedence over the recalculation. The recalculation is best understood as a check based on the posted group means, standard deviations, and sample sizes, not as a replacement for the sponsor’s analysis or a reconstruction of its model.

The record does not provide enough detail to identify the source of every discrepancy. It does not report the model output, adjusted estimates, covariate-adjusted confidence intervals, or full analysis code and specifications. Consequently, readers can distinguish the sponsor-reported tests from the unadjusted recalculations, but cannot fully reconcile them from the registry record alone.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists 7 outcome measures and 84 analyses. The primary endpoint description names an ANCOVA model and a significance criterion of P < 0.05, but the record does not report a family-wise error strategy, false-discovery procedure, hierarchical testing plan, or other adjustment for the many comparisons. It is therefore unclear whether the posted p-values were adjusted for multiplicity. When multiple treatment groups and outcomes are examined, an unadjusted p-value should not be interpreted as if it were the only test conducted.

The registry identifies the primary population as ITT and defines it as subjects who received at least one dose of test article. It does not provide a fuller account of whether all randomized participants were included, how exclusions were handled, or how this population relates to the conventional meaning of intention-to-treat. Participant flow by randomized group and reasons for missing measurements are not reported in the registry record.

Missing-data methods are also not described in enough detail to assess their impact. The outcome was measured weekly for up to 12 weeks or until closure, and the record does not explain how incomplete follow-up, missed visits, early closure, or other unavailable measurements were incorporated into the primary average. Sensitivity analyses for missing data are not reported. For the time-to-event outcome, censoring details and checks of model assumptions are not reported.

The registry record does not report whether interim analyses were planned or conducted, nor does it report the original sample-size justification or the complete statistical analysis plan. These omissions limit assessment of prespecification and the relationship between planned and reported analyses. They do not establish that such procedures were absent; they mean the details are not reported in the registry record.

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 3% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: pneumonia pneumococcal (2.3%), neoplasm malignant (2.3%), alcohol withdrawal syndrome (2.3%), acute respiratory failure (2.3%), peripheral vascular disorder (2.3%).

The posted adverse-event summary gives the number of participants at risk and the number affected by serious and other adverse events in each group. Serious adverse events affected 4 of 50 in the vehicle group, 4 of 46 in low Q14D, 3 of 43 in low Q7D, 3 of 43 in high Q14D, and 2 of 45 in high Q7D. Other adverse events affected 26 of 50, 15 of 46, 19 of 43, 16 of 44, and 17 of 45, respectively, across vehicle, low Q14D, low Q7D, high Q14D, and high Q7D.

These are descriptive counts, not adjusted comparisons. They do not establish whether differences between groups are meaningful, and the record does not give event-level exposure time or a formal comparative safety analysis. The registry lists several serious-event terms with percentages, but does not provide enough context in the posted summary to infer causation. Death counts are not reported in the registry record. These figures describe the posted safety summary and should not be interpreted as a complete account of all safety information.

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

The results describe a randomized comparison of four HP802-247 dose-and-frequency schedules with vehicle in people with venous leg ulcers. In each arm, the posted primary mean percent change from baseline was negative. The sponsor’s reported pairwise tests and the unadjusted recalculations provide different statistical summaries, and the registry record does not fully reconcile them. The sponsor’s own analysis takes precedence over the recalculation, while the recalculation offers a transparent but unadjusted comparison from the posted summaries.

These results do not establish that a particular dose or schedule is best. The study compared multiple regimens, and the record does not report a multiplicity adjustment or the complete prespecified analysis plan. The group means also summarize averages and do not describe the range of individual outcomes. Confidence intervals convey statistical uncertainty, but they do not determine whether a difference is important in practice.

The primary endpoint concerns change in target wound area over repeated measurements. It is not the same outcome as complete wound closure, time to closure, pain, or other aspects of the condition. Some secondary results are posted, and other listed outcomes have no numerical results in the registry record. Missing outcome results cannot be inferred from the posted primary results.

The registry record also leaves important questions about missing data, participant flow, analysis populations, and the original sample-size rationale unanswered. For those reasons, the posted findings should be read as the results documented in the registry, with their stated methods and reporting limits. They do not by themselves establish a broader conclusion beyond the measured outcomes and comparisons in this trial.

18. Why This Trial Matters Statistically

This trial is statistically informative because its design varies both concentration and dosing frequency while retaining a vehicle comparison. That structure makes it possible to examine several regimen-specific contrasts, but it also creates a multiplicity challenge. A collection of pairwise results needs a clearly described analysis strategy so readers can understand which comparisons were primary and how the overall chance of false-positive findings was managed. The registry record does not report that strategy.

The difference between the stated ANCOVA primary model and the listed sponsor-reported t-tests is another important reporting issue. Adjusted and unadjusted comparisons answer related but not identical questions. The recalculations from summary statistics can make the arithmetic comparison more transparent, but they cannot reproduce the specified covariate-adjusted analysis. Where those results differ, the sponsor’s own analysis takes precedence, while the lack of model detail limits independent reconciliation.

The study also illustrates why effect estimates and precision matter alongside p-values. Group means, variability, and confidence intervals help show both direction and uncertainty. The secondary time-to-event analysis uses a different estimand and modeling framework, so it should not be treated as interchangeable with mean wound-area change. Finally, incomplete reporting of secondary outcomes and missing-data procedures constrains how comprehensively readers can assess the outcome pattern. These issues are relevant to statistical interpretation even when a trial is randomized and masked.

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 arise from the registry record itself. The posted primary analysis description specifies ANCOVA, but the reported pairwise primary tests are identified as two-sided t-tests. The record does not provide enough model output or detail to reconcile that difference with the unadjusted recalculations. The stated significance criterion is given, but no multiplicity procedure is reported despite the record listing 84 analyses.

Participant flow and missing-data handling are not described in sufficient detail to determine how the primary average was calculated for participants with incomplete weekly measurements or early closure. The registry’s definition of the ITT population is limited to subjects who received at least one dose, and a fuller account of the analysis population is not reported. The original sample-size justification, randomization procedures, allocation concealment, and details of masking are not reported in the registry record.

Secondary outcome reporting is incomplete. The registry lists outcomes relating to area change, closure, pain, and time to closure, but numerical results are not posted for every listed outcome. Some time-to-closure interval limits are also absent. The Cox model assumptions and censoring details are not reported. These gaps make it difficult to assess consistency across endpoints or the robustness of estimates.

The results apply to the specified trial population and measured outcomes; the registry does not provide enough information to assess generalizability beyond that setting. The study’s 16-week description and the primary measurement period of up to 12 weeks are both reported, but the record does not give a fuller account of follow-up after the primary treatment period. These limitations concern what the registry reports and should not be taken as proof that unreported procedures or analyses did not occur.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Dose Finding Study of HP802-247 in Venous Leg Ulcers — NCT00852995.
• Registry record last updated 2016-10-24; status last verified 2016-09.
• Results first posted 2016-03-14.
• 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

NCT00852995 is a completed Phase II randomized, triple-masked, parallel-group dose-finding study of HP802-247 in venous leg ulcers, sponsored by Healthpoint. The registry lists enrollment of 228 and five arms: low and high HP802-247 given weekly or every other week, plus vehicle at each visit. Standard care is described in the study summary.

The primary outcome is average percent change from baseline in target wound area during the double-blind treatment period, measured weekly for up to 12 weeks or until closure. The sponsor reports pairwise two-sided t-test results against vehicle, while the primary analysis description specifies ANCOVA. Unadjusted recalculations are available, but the sponsor’s own analysis takes precedence where results differ. Secondary outcomes cover wound area, closure, pain, and time to closure; numerical results are not reported for every listed measure. Multiplicity procedures, missing-data handling, and the original sample-size justification are not reported in the registry record.