Efficacy and Safety Study of DX-88 to Treat Acute Attacks of Hereditary Angioedema (HAE): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Efficacy and Safety Study of DX-88 to Treat Acute Attacks of Hereditary Angioedema (HAE) (NCT00262080), a randomized phase 3 study. The primary outcome is Treatment Outcome Score at 4 Hours Post-Dose.

2. Clinical Question

The registry describes a study of whether a subcutaneous dose of DX-88 was safe and relieved symptoms during acute attacks. The primary endpoint was a comprehensive symptom-response score. It reflects patients’ assessment of changes from baseline across involved anatomic sites, with baseline severity used to weight the site scores. A score of 30 or higher was designated as clinically meaningful improvement.

The posted primary outcome compares arm means, while the sponsor’s reported inferential analysis used a non-parametric Wilcoxon Rank Sum test. These answer related but not identical statistical questions: the mean difference expresses the average separation in the posted scores, whereas the rank-sum test compares the distributions of scores through their ranks. The registry reports a mean of 49.5 for ecallantide and 18.5 for placebo, with 36 participants in each primary arm. The registry record does not explain how these analysis counts relate to the overall enrollment of 91.

The clinical question is limited to the acute, double-blind assessment at 4 hours post-dose. A secondary outcome addressed time to significant improvement in overall response, but the primary result alone does not describe the timing or persistence of any response.

3. Trial Design

This was a phase 3, randomized, parallel-group study with quadruple masking and a placebo control. The official title describes a double-blind, placebo-controlled study with 72 patients randomized 1:1, followed by a repeat-dosing phase. The registry lists enrollment of 91 and status as completed. The record does not explain the relationship between the 72 patients in the title and the enrollment figure of 91.

The double-blind comparison assigned participants to ecallantide or placebo. Ecallantide was given as 30 mg in three subcutaneous injections; placebo was phosphate buffer saline at pH 7.0, also given in three subcutaneous injections. The primary outcome was assessed 4 hours post-dose during the double-blind part. The record also lists a repeat-dosing phase for ecallantide. Its safety group included 67 participants, but further details of that phase’s protocol are not reported in the registry record.

The primary outcome analysis lists 36 participants in each arm. Its population is described as ITT as treated: two participants randomized at the same study center on the same day received treatment opposite to their randomized assignment. Their data were analyzed according to treatment received. This distinction matters because the posted analysis groups are based on actual treatment rather than the original randomized assignment for those participants.

The registry lists two secondary outcomes: change from baseline in mean Symptom Complex Severity score at 4 hours post-dose, and time to significant improvement in overall response. It reports seven outcome measures and three analyses. More detailed information about the original statistical analysis plan, allocation procedures, concealment, and the design assumptions for the study is not reported in the registry record.

The listed start and primary completion dates are both 2005-12-31. Those dates describe the record and do not provide detail about recruitment duration, follow-up schedules, or when the repeat-dosing phase occurred. Such details 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: Patients were screened in advance of presenting with an Hereditary Angioedema (HAE) attack but were randomized only upon attack.

Double Blind Treatment Period

Reasons for not completing this period:

Repeat Dose Treatment Period

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: ITT as treated: two patients randomized on the same day at the same study center were administered treatment opposite to their randomized treatment assignment. Data were analyzed based on actual treatment received. Imputation was used to account for emerging symptoms and medical intervention. Best possible score = 100; worst possible score = -100.

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 Treatment Outcome Score at 4 Hours Post-Dose, measured over 4 hours post-dose (DOUBLE-BLIND PART).

The primary endpoint was the Treatment Outcome Score at 4 hours post-dose in the double-blind part. The record describes this as a validated, comprehensive measure of symptom response. Participants assessed their response through changes from baseline in symptom severity at the anatomic sites involved in the attack. Responses were recorded on a categorical scale ranging from significant improvement at 100 to significant worsening at -100.

Scores for the involved sites were weighted by baseline severity, then averaged to obtain a participant’s Treatment Outcome Score. This construction is intended to reflect both symptom change and the severity of affected sites rather than treating every site as equally important. The registry identifies a score of 30 or higher as clinically meaningful improvement. That threshold helps contextualize the scale, but it does not mean that an arm average describes how many individual participants reached the threshold.

The endpoint was used to compare symptom response at a specified early assessment time. The posted arm summaries are means and standard deviations, which describe the average score and the spread of scores around that average. The ecallantide arm mean was 49.5, and the placebo arm mean was 18.5. These group summaries do not show the individual score distribution or the proportion of participants who improved by a particular amount.

The registry says imputation was used to account for emerging symptoms and medical intervention. The specific imputation procedure and its assumptions are not reported in the registry record. The endpoint therefore has a defined clinical interpretation, while the details needed to fully assess how missing or intercurrent observations affected it are limited.

7. Results Posted in the Registry

• Ecallantide: mean 49.50 versus 18.50 on control; difference 31.00 (95% CI 1.55 to 60.45), standardized effect d = 0.49; z-test p = 0.039.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary outcome is a continuous measure, and the registry reports an arm mean and standard deviation for each treatment group. A mean gives the arithmetic average of the participant scores. A standard deviation describes how dispersed the observations are around that average. In general, a small standard deviation means scores cluster more closely around the mean, while a large standard deviation means scores are more spread out. The standard deviations are 59.43 for ecallantide and 67.78 for placebo, indicating considerable spread on the score scale.

What does the mean difference describe?

The recalculated mean difference is 31.0 units, with the ecallantide mean higher than the placebo mean. A difference in means is an estimate of the average separation between two groups on the measured scale. It does not say that every participant had a score 31.0 units higher, nor does it describe the distribution of individual responses. The recalculation is unadjusted and is based on the posted summary statistics; it is not a replacement for an analysis that accounts for participant-level data or other modeling features.

In general, a confidence interval expresses uncertainty around an estimated effect under the method used to construct it. Its width reflects both the amount of information and the variability in the data, as well as the chosen confidence level. A wider interval permits a broader range of effect sizes than a narrower interval. The recalculated interval extends from 1.553 to 60.45. The sponsor-reported analysis identifies a 95% confidence level, but does not report interval limits for that analysis.

Why are the two p-values different?

The sponsor’s reported test was a non-parametric Wilcoxon Rank Sum test, with p = 0.037. A rank-based test orders observations and compares the ranks between groups. In general, this approach can be useful when an analysis is framed around the distribution of observations rather than a direct comparison of means, and it does not require the test to be expressed as a difference between arithmetic means. The posted report does not give the participant-level data or additional details of the test implementation.

The recalculated p = 0.039 is an unadjusted result associated with the simple re-calculation from the posted summary statistics. It is not the same test as the sponsor’s rank-sum procedure. Small numerical differences between results from different statistical methods are possible because the methods use the data differently. A p-value describes how compatible the observed data are with a specified null model, under the assumptions of the test. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of an effect.

What is over-dispersion, and does it apply?

Over-dispersion is a general concept most often used for count outcomes: it means the observed variability is greater than a model assumes. The primary endpoint is a continuous score, not a count. The registry provides standard deviations but does not report an over-dispersion assessment. For this endpoint, the practical statistical concern visible in the summary is the broad spread of scores within each group, which contributes to uncertainty in the estimated group difference.

What does the rank-sum test establish?

In general, a rank-sum test evaluates whether observations in one group tend to be ranked higher or lower than observations in another group. It is not automatically a test of the difference between medians, and it does not directly estimate the mean difference. The reported p-value should therefore be read as the result of the sponsor’s specified rank-based comparison, not as a p-value testing the recalculated mean difference. The record does not report a parameter estimate or confidence interval for the rank-sum analysis.

How should the analysis population be understood?

The registry labels the primary analysis population ITT as treated. It states that two participants randomized on the same day at the same center received treatment opposite to their randomized assignments, and that the data were analyzed according to the treatment actually received. In general, an as-treated analysis groups participants by the treatment received, while an intention-to-treat analysis ordinarily retains participants in their randomized groups. The label used in the record and the described handling should both be considered; the registry does not provide a separate randomized-assignment result for comparison.

Imputation was used to account for emerging symptoms and medical intervention. In general, imputation replaces or otherwise accounts for unavailable or altered observations according to specified assumptions. Those assumptions can affect an estimate, particularly when missingness or additional intervention is related to the outcome. The registry does not report the imputation method, the number of affected observations, or sensitivity analyses. The reason for imputation is stated, but its detailed statistical implementation is not reported in the registry record.

What is not available about the analysis plan?

The record reports seven outcome measures, three analyses, and two posted secondary outcomes. It does not describe whether or how statistical testing was adjusted for the number of outcomes, whether there were planned interim analyses, or what original sample-size justification was used. The sample-size figures associated with the observed effect are planning illustrations, not evidence about the original trial’s design. Detailed model specifications and the full statistical analysis plan are not reported in the registry record. These gaps constrain how completely the reported tests can be evaluated.

10. Confidence Intervals and Precision

The recalculated mean difference is 31.0 units, with an interval from 1.553 to 60.45. The interval is wide enough to accommodate substantially different magnitudes of separation between the groups. Its lower end is near zero relative to the scale of the point estimate, while the upper end permits a much larger difference. This is a reason to distinguish the estimated direction from precision about the effect size.

The sponsor-reported analysis identifies a 95% confidence level, but its confidence interval limits are not reported. The interval limits available for the mean difference come from the unadjusted recalculation; the record does not identify a confidence level for those limits. In general, a confidence interval is constructed by a method that would cover the target parameter at its stated rate over repeated use under the method’s assumptions. It does not mean that there is a 95% probability that this particular interval contains the true value.

The group standard deviations, 59.43 for ecallantide and 67.78 for placebo, show that scores varied considerably within both arms. When observations are dispersed, a given group size tends to provide less precise information about the mean than more tightly clustered observations would. The primary analysis included 36 participants per arm. The interval therefore needs to be read together with both the sample sizes and the observed spread, rather than relying only on the point estimate.

The score’s clinically meaningful threshold of 30 or higher applies to an individual score as described by the registry. The mean-difference interval is on the scale of the between-group average difference, not a confidence interval for the percentage of individuals exceeding that threshold. The available primary summary does not report the individual-level response proportion or an interval for it.

The sponsor’s rank-sum result has p = 0.037 but no reported effect estimate or interval limits. A p-value alone does not convey the range of plausible effect sizes. The available mean-difference interval provides information about precision for the unadjusted average contrast, while the sponsor’s analysis supplies a different inferential result. Neither should be treated as resolving uncertainty beyond the analysis and population to which it applies.

11. 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 describe participants per arm for this continuous endpoint, not total events. They use the observed mean difference of 31.0 as a reference and consider planning for 100% of the observed effect, 75% of the observed effect, or 50% of the observed effect. For 100% of the observed effect, the illustration gives 67 participants per arm for 80% power and 89 participants per arm for 90% power. For 75% of the observed effect, it gives 118 participants per arm for 80% power and 158 participants per arm for 90% power. For 50% of the observed effect, it gives 266 participants per arm for 80% power and 356 participants per arm for 90% power.

The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is the stated fraction of the observed effect. The record does not report the original trial’s sample-size assumptions or justification, so these values should not be read as the study’s original design target.

In plain terms, the 80% power column gives the per-arm sample size indicated by the planning calculation when the assumed effect is the chosen fraction of the observed difference and the other assumptions hold. The 90% power column uses a higher target probability of detecting an effect of that size under those assumptions. Higher target power generally requires more participants. Similarly, planning for a smaller effect requires more participants because a smaller group separation is harder to distinguish from variability. These figures are planning illustrations, not observed power.

12. 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 = 31.000; pooled standard deviation σ = 63.742.
2. n = 2 × (1.96 + 0.842)² × 63.742² / 31.000² = 66.4, rounded up to 67 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 <- 31                      # observed difference in means
sigma <- 63.7418751685264                     # 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(262080)
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 = 67 (80% power), 89 (90% power)
 75% of observed effect: n per arm = 118 (80% power), 158 (90% power)
 50% of observed effect: n per arm = 266 (80% power), 356 (90% power)
power.t.test: 67.3 
Simulated power at n = 67 per arm: 0.800 (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.

13. Analyses Reported by the Sponsor

The sponsor’s reported primary comparison used a non-parametric Wilcoxon Rank Sum test and gave p = 0.037. The reported analysis identifies a 95% confidence level, but does not provide a parameter estimate or confidence interval limits. The rank-sum test compares the groups using ranks, rather than directly estimating the difference in arithmetic means.

The unadjusted recalculation from the posted arm summaries gives a mean difference of 31.0 units, an interval from 1.553 to 60.45, and p = 0.039. This recalculation addresses the mean contrast using the reported means and standard deviations; it is not a reproduction of the sponsor’s rank-based test. The values answer related questions, but they should not be treated as interchangeable results.

The record does not flag a discrepancy between the reported result and the recalculation. The sponsor’s analysis remains the trial’s reported analysis, while the recalculation is a separate summary-statistic-based comparison. The available information does not establish the sponsor’s detailed test implementation, the analysis plan’s handling of multiplicity, or whether additional adjusted analyses were conducted. The two p-values should therefore be presented with their methods clearly distinguished, not combined into a single result.

14. Multiplicity, Missing Data and Analysis Populations

The registry lists seven outcome measures and three analyses. It names two secondary outcomes: change from baseline in mean Symptom Complex Severity score at 4 hours post-dose and time to significant improvement in overall response. The primary outcome was the Treatment Outcome Score at 4 hours post-dose. The registry record does not report whether the statistical plan adjusted for testing multiple outcomes or analyses, how any adjustment was performed, or which outcome was designated as the sole confirmatory test.

Multiplicity matters in general because conducting multiple statistical tests can increase the chance of at least one apparently notable result even when the effects being tested are absent. Adjustment procedures can address this issue, but the record does not identify one. The sponsor-reported p-value should consequently be read as the reported result for its analysis; the available information does not establish its status within a broader testing hierarchy.

The primary analysis population is described as ITT as treated. The record explains that two participants randomized at the same center on the same day received treatment opposite to their randomized assignment and were analyzed according to actual treatment received. This description clarifies how those participants were grouped, but no result based on their original randomized assignments is reported in the primary summary. The effect of the analysis-population choice cannot be assessed without that comparison.

Imputation was used to account for emerging symptoms and medical intervention. The reason for using imputation is stated, but its method, assumptions, and the number of observations affected are not reported in the registry record. No sensitivity analyses are described in the available information. In general, sensitivity analyses can show whether a conclusion changes under reasonable alternative assumptions about unavailable or modified observations. Without them, the robustness of the primary result to the imputation approach cannot be evaluated from this record.

Interim analyses, stopping rules, and detailed missing-data procedures are not reported in the registry record. The sample-size illustration based on the observed effect is not the trial’s original sample-size justification. These omissions do not invalidate the posted result, but they limit assessment of how the analysis was planned and how uncertainty from multiple testing and incomplete or altered observations was handled.

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: hereditary angioedema (8.3%), anaphylactic reaction (1.5%), anxiety (1.5%), colitis (1.5%), concussion (1.5%).

The registry lists serious adverse events for 36 participants in the double-blind ecallantide group, 36 in the double-blind placebo group, and 67 in the repeat-dosing ecallantide group. The corresponding counts of participants with serious adverse events are 3, 2, and 7. These are group-specific counts; they should be read alongside the group sizes and phases, rather than combined as though all participants belonged to a single comparison.

For other adverse events, the record lists 13 affected participants among 36 in the double-blind ecallantide group, 7 among 36 in the double-blind placebo group, and 22 among 67 in the repeat-dosing ecallantide group. These counts concern the registry’s other-adverse-event category and are distinct from the serious-event counts. The record does not give event-level detail for every participant in these figures, so the counts should not be treated as counts of unique event types or as measures of event severity beyond the stated categories.

The listed serious adverse event terms include Hereditary Angioedema at 8.3%, and Anaphylactic Reaction, Anxiety, Colitis, Concussion, and Contusion at 1.5% each. The record does not clarify the denominators or whether these percentages refer to participants or events, so they should be interpreted as the posted term percentages without deriving additional rates from them. Deaths are not reported in the registry record. Safety counts from the repeat-dosing phase are presented separately from the double-blind comparison and do not constitute a randomized placebo comparison for that phase.

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

The posted primary result shows a higher mean Treatment Outcome Score at 4 hours post-dose in the ecallantide group than in the placebo group: 49.5 versus 18.5. The recalculated mean difference is 31.0 units, and the sponsor’s rank-sum analysis reports p = 0.037. The unadjusted recalculation reports p = 0.039. These results describe the observed comparison and its statistical analysis; they do not, by themselves, establish a treatment recommendation or settle broader questions about clinical benefit.

The estimate is not perfectly precise. The recalculated interval from 1.553 to 60.45 covers a broad range of possible mean differences. The sponsor’s reported analysis does not give interval limits, and its 95% confidence level should not be assigned to the recalculated interval without a stated basis. The primary scores also show substantial variability, with standard deviations of 59.43 and 67.78. Thus, the group average does not represent every participant’s experience.

The registry’s threshold of 30 or higher is defined as clinically meaningful improvement for an individual Treatment Outcome Score. The ecallantide group mean is above that threshold and the placebo group mean is below it. Those group-level means do not reveal the fraction of participants who reached the threshold, how responses were distributed, or whether particular participants worsened. The record’s primary summary does not provide those individual-level details.

The analysis concerns an assessment at 4 hours in the double-blind part. It cannot answer, from the primary result alone, how long any improvement lasted or what happened at later assessments. A secondary outcome concerns time to significant improvement, but the primary result does not substitute for that outcome’s results. The record also includes a repeat-dosing phase, whose safety group is separate from the double-blind comparison.

Interpretation is further bounded by the as-treated handling of two participants, the use of imputation for emerging symptoms and medical intervention, and the absence of reported details about those procedures. The record also does not state whether multiplicity adjustment was used. These features affect how fully the statistical evidence can be evaluated, even though the primary comparison and its reported result are identifiable.

17. Why This Trial Matters Statistically

This trial is statistically informative because it illustrates the difference between a clinical endpoint’s definition and the statistical summaries used to compare groups. The Treatment Outcome Score combines symptom changes across involved anatomic sites, weights them by baseline severity, and produces a continuous score. The mean difference summarizes average separation, while the sponsor’s rank-sum test compares observations using ranks. Both can be relevant, but they do not estimate exactly the same quantity.

The result also shows why an effect estimate and a test result should be read together. The recalculated mean difference of 31.0 gives the estimated average separation, while the interval from 1.553 to 60.45 communicates substantial uncertainty about its magnitude. The sponsor p-value of 0.037 indicates the result of the reported rank-based test, but does not show the size of the difference or its precision. A statistically notable p-value does not remove uncertainty about the effect estimate.

The clinical threshold adds another useful distinction. A score of 30 or higher is defined as meaningful improvement for an individual, but the arm means cannot tell readers how many individuals crossed that threshold. This is a common interpretive issue for continuous outcomes: a summary of averages can be informative while leaving the response distribution and individual-level outcomes unresolved.

The record’s analysis population and imputation note also matter. Two participants were analyzed according to the treatment received rather than their randomized assignment, and imputation addressed emerging symptoms and medical intervention. The details of these choices are not reported. Explicitly describing them helps readers understand which comparison the posted result represents and where methodological uncertainty remains.

Finally, the enrollment and primary analysis counts are not the same, and the registry does not explain their relationship. The official title describes 72 randomized participants, while the record lists enrollment of 91 and 36 participants in each primary arm. Recognizing that distinction prevents readers from assuming that one count necessarily describes every phase or analysis population. Overall, the record supports careful interpretation of the reported comparison, not a conclusion beyond its endpoint, population, and measurement time.

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 in this trial record. The enrollment count is 91, the official title describes 72 patients randomized 1:1, and the primary outcome has 36 participants in each arm. The record does not explain how these counts relate to each other or to participation in the repeat-dosing phase. The primary analysis population is described as ITT as treated, and two participants received treatment opposite to their randomized assignment and were analyzed according to treatment received. A randomized-assignment analysis is not reported in the primary summary.

The primary endpoint is a composite score based on symptom changes at involved anatomic sites and is assessed at 4 hours post-dose. That makes the endpoint a specific snapshot of response. The primary result does not establish how persistent any change was, and the group means do not show individual response patterns or the number of participants who met the score threshold of 30 or higher.

The score summaries show substantial variability, and the recalculated interval spans from 1.553 to 60.45. The estimate is therefore not narrowly determined by the posted data. The sponsor reports a rank-sum p-value but no corresponding effect estimate or interval limits. The unadjusted recalculation is not the sponsor’s test and should not be substituted for it.

The registry states that imputation was used for emerging symptoms and medical intervention, but does not report its method, assumptions, or sensitivity analyses. It also does not report whether multiple testing was adjusted, whether interim analyses were conducted, or the original sample-size justification. Detailed information about the repeat-dosing protocol is not reported in the registry record. These gaps limit assessment of analysis robustness, multiplicity, and the relationship between the phases.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Efficacy and Safety Study of DX-88 to Treat Acute Attacks of Hereditary Angioedema (HAE) — NCT00262080.
• Registry record last updated 2021-06-11; status last verified 2021-06.
• Results first posted 2010-05-11.
• 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

This completed phase 3 randomized, parallel-group, quadruple-masked study compared ecallantide with placebo for acute hereditary angioedema attacks. Ecallantide was administered as 30 mg in three subcutaneous injections; placebo was phosphate buffer saline in three injections. The primary outcome was Treatment Outcome Score at 4 hours post-dose during the double-blind part.

The primary analysis included 36 participants per arm. Mean scores were 49.5 for ecallantide and 18.5 for placebo. The sponsor-reported Wilcoxon Rank Sum test gave p = 0.037. The unadjusted recalculation gave a mean difference of 31.0, an interval from 1.553 to 60.45, and p = 0.039. The registry describes an ITT as-treated population and notes imputation for emerging symptoms and medical intervention.

The record lists two secondary outcomes and a repeat-dosing phase. It does not explain the relationship between overall enrollment of 91, the 72 patients described in the official title, and the primary analysis counts. Further details on multiplicity, imputation, and the original sample-size justification are not reported in the registry record.