Study of Two Doses of Crizanlizumab Versus Placebo in Adolescent and Adult Sickle Cell Disease Patients: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study of Two Doses of Crizanlizumab Versus Placebo in Adolescent and Adult Sickle Cell Disease Patients (NCT03814746), a randomized phase 3 study. The primary outcome is Annualized Rate of Vaso-occlusive Crisis (VOC) Events Leading to a Healthcare Visit.

2. Clinical Question

3. Trial Design

STAND was a phase III, randomized, multicenter, parallel-group study comparing two doses of crizanlizumab with placebo in adolescent and adult patients with sickle cell disease. The official title describes the trial as double-blind, while the registry record lists quadruple masking. The specific roles included in the registry's masking designation are not reported in the registry record.

Participants were assigned to crizanlizumab at 5.0 mg/kg, crizanlizumab at 7.5 mg/kg, or placebo. The study was intended to assess efficacy and safety in patients with a history of vaso-occlusive crisis leading to a healthcare visit, with or without hydroxyurea or hydroxycarbamide therapy. The registry record reports 253 enrolled participants. The primary outcome summaries use arm-specific analysis counts of 84, 83, and 85, respectively; the record does not explain the difference between enrollment and these outcome counts.

The registry lists a study start date of 2019-07-26 and primary completion on 2022-08-31. Its status is active, not recruiting. Further details about recruitment, treatment duration, visit schedules, or allocation procedures are not reported in the registry record. Although the study title identifies two active doses and placebo, details such as the randomization ratio and any stratification factors are not reported in the registry record.

The primary endpoint covers one year and is an annualized event rate, rather than simply a count of participants who experienced any crisis. Secondary outcomes include additional crisis-rate measures, duration of crises, freedom from crises, time to crises, and healthcare use. The registry lists 24 outcome measures and 16 analyses, but a full statistical analysis plan is 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: Screening assessments were done within 1 to 28 days prior to Week 1 Day 1. Re-screening of subjects was only allowed if the subject was not randomized before.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The FAS comprises all participants to whom study treatment has been assigned by randomization.

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: The FAS comprises all participants to whom study treatment has been assigned by randomization.

6. Primary Endpoint

The registry lists the primary outcome as Annualized Rate of Vaso-occlusive Crisis (VOC) Events Leading to a Healthcare Visit, measured over 1 year.

The primary endpoint is the annualized rate of vaso-occlusive crisis events that led to a healthcare visit, measured over a one-year timeframe. The registry defines a vaso-occlusive crisis as a pain crisis with acute pain and no other medically determined explanation apart from vaso-occlusion, requiring oral or parenteral opioids or a parenteral non-steroidal anti-inflammatory drug. It also includes complicated crises such as acute chest syndrome, priapism, and hepatic or splenic sequestration.

A healthcare visit includes a visit to a medical facility, such as an emergency room or hospital, or an office visit that includes pain management in situ. The registry annualizes the number of events according to the number of observed days, so the result represents an event rate per year rather than a raw count over identical observation time for every participant.

Annualized rates are useful when participants contribute different amounts of observation time. However, they do not by themselves describe how many participants experienced at least one event, how events were distributed among participants, or how long each crisis lasted. Those questions are addressed by distinct secondary outcomes. The primary analysis population is the full analysis set, defined in the record as all participants assigned study treatment by randomization.

The observation period is defined from randomization to the earliest of specified stopping points: the last dose date plus 27 days after treatment discontinuation, a date related to initiation or discontinuation of certain other sickle cell therapies, or randomization plus 365 days. The registry's endpoint description supplies this operational definition; additional details on how changes in observation time were handled statistically are not reported in the registry record.

7. Results Posted in the Registry

• Crizanlizumab (SEG101) at 5.0 mg/kg: 2.50 versus 2.10 (number of events per year) on control; rate ratio 1.19 (95% CI 0.98–1.45, approximate, Poisson model); p ≈ 0.087.
• Crizanlizumab (SEG101) at 7.5 mg/kg: 1.90 versus 2.10 (number of events per year) on control; rate ratio 0.90 (95% CI 0.73–1.12, approximate, Poisson model); p ≈ 0.360.

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.

Annualized Rate of All VOCs Leading to a Healthcare Visit and Treated at Home Over the First-year Post Randomization (Key Secondary)

• Endpoint type: Event rate: events per unit of follow-up, compared as a rate ratio.
• Test: Poisson rate ratio, based on the estimated number of events and follow-up time.
• Result:
  • Crizanlizumab (SEG101) at 5.0 mg/kg: 4.50 versus 3.70 (number of events per year) on control; rate ratio 1.22 (95% CI 1.05–1.41, approximate, Poisson model); p ≈ 0.010.
  • Crizanlizumab (SEG101) at 7.5 mg/kg: 3.10 versus 3.70 (number of events per year) on control; rate ratio 0.84 (95% CI 0.71–0.99, approximate, Poisson model); p ≈ 0.035.
• Interpretation:
  • The 95% confidence interval excludes no difference (a ratio of 1), so the event rate is statistically higher for Crizanlizumab (SEG101) at 5.0 mg/kg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference (a ratio of 1), so the event rate is statistically lower for Crizanlizumab (SEG101) at 7.5 mg/kg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Mean Duration of VOCs Leading to a Healthcare Visit Over the First-year Post Randomization

• 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:
  • Crizanlizumab (SEG101) at 5.0 mg/kg: mean 7.70 versus 6.60 on control; difference 1.10 (95% CI -1.23 to 3.43), standardized effect d = 0.17; z-test p = 0.356.
  • Crizanlizumab (SEG101) at 7.5 mg/kg: mean 6.00 versus 6.60 on control; difference -0.60 (95% CI -2.56 to 1.36), standardized effect d = -0.12; z-test p = 0.549.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Crizanlizumab (SEG101) at 5.0 mg/kg 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 Crizanlizumab (SEG101) at 7.5 mg/kg and the control. The interval gives the range of effects that remain compatible with the data.

Number of Participants Free From VOCs Leading to a Healthcare Visit Over the First-year Post Randomization

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Crizanlizumab (SEG101) at 5.0 mg/kg: 29.8% (25/84) versus 40.0% (34/85) on control; risk difference -10.2 percentage points (95% CI -24.5 to 4.0), risk ratio 0.74 (0.49–1.13); unadjusted two-proportion z-test p = 0.163.
  • Crizanlizumab (SEG101) at 7.5 mg/kg: 37.3% (31/83) versus 40.0% (34/85) on control; risk difference -2.7 percentage points (95% CI -17.4 to 12.1), risk ratio 0.93 (0.64–1.37); unadjusted two-proportion z-test p = 0.724.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Crizanlizumab (SEG101) at 5.0 mg/kg 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 Crizanlizumab (SEG101) at 7.5 mg/kg and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes extend the primary question in several directions: they include crises treated at home, crisis duration, whether participants remained free of a healthcare-visit crisis, time to first and second crises, and healthcare use. The posted secondary results therefore describe related but distinct aspects of crisis burden and service use. They should not be treated as interchangeable versions of the primary event-rate endpoint.

Across the posted rate summaries, the dose-specific group patterns are not uniformly aligned with a simple reduction in events relative to placebo. The secondary comparisons also differ in outcome definition and analysis method, and the posted values alone do not establish a consistent overall pattern. Their relationship to the primary result is best understood as additional descriptive evidence, not as a replacement for the sponsor's primary negative binomial comparisons.

Some secondary outcomes are supported by sponsor-reported analyses, while others have posted arm summaries without a corresponding reported analysis. Where a sponsor analysis is absent, an unadjusted contrast based on summary statistics is especially limited: it may not match the planned analysis, and it cannot account for analysis details not present in the registry record. The registry record lists 23 secondary outcomes as posted, but not all the secondary endpoints named in the record have detailed results in the information available for this discussion.

Multiplicity is another reason to give unadjusted secondary results less weight. When many outcomes or comparisons are examined, the chance of seeing apparently notable results by chance can increase. General explanation: adjustment procedures or a prespecified testing hierarchy can address this issue, but the multiplicity plan is not reported in the registry record. Accordingly, secondary p-values calculated from summary statistics should be treated as exploratory rather than as confirmatory evidence, and no isolated secondary finding should overturn the uncertainty in the primary result.

Taken together, the secondary outcomes broaden the clinical description but do not resolve the primary comparison. They may suggest questions for further evaluation, but the record does not report a comprehensive multiplicity-adjusted synthesis that would support a single overall conclusion across all endpoints.

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

• Annualized Rate of All VOCs Leading to a Healthcare Visit and Treated at Home Over the First-year Post Randomization (Key Secondary)
• Annualized Rate of All VOCs Leading to a Healthcare Visit and Treated at Home Over 5 Years Post Randomization (Key Secondary)
• Mean Duration of VOCs Leading to a Healthcare Visit Over the First-year Post Randomization
• Number of Participants Free From VOCs Leading to a Healthcare Visit Over the First-year Post Randomization
• Percentage of Participants Free From VOCs Leading to a Healthcare Visit Over the First-year Post Randomization
• Time to First and Second VOCs Leading to a Healthcare Visit Over the First-year Post Randomization
• Annualized Rate of Visits to Clinic, Emergency Room (ER) and Hospitalizations, Both Overall and VOC-related Over the First-year Post-randomization
• Annualized Days of Visits to Clinic, Emergency Room (ER) and Hospitalizations, Both Overall and VOC-related Over the First-year Post-randomization

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is a rate, because it counts recurrent events in relation to time under observation. A rate ratio compares the event rate in one treatment group with the rate in the comparator group. A ratio of 1 represents equal rates; a ratio greater than 1 indicates a higher estimated rate in the treatment group, and a ratio less than 1 indicates a lower estimated rate. These descriptions concern the direction of the statistical estimate and do not establish a causal or clinical conclusion by themselves.

Why model event rates?

The sponsor reports negative binomial regression for the primary comparisons. This is a model commonly used for count outcomes when the counts vary more than a simple Poisson model would expect. General explanation: Poisson models assume a particular relationship between the mean and variance of counts. When the data show over-dispersion—more variation than that assumption allows—a negative binomial model can allow the variance to be larger than the mean. This matters because a model that does not adequately represent variability can produce uncertainty estimates that are too narrow or otherwise poorly calibrated. The registry record does not report the model's covariates, offset specification, or diagnostic checks.

The code-based recalculation uses posted group summaries and a simple Poisson approach. It is an unadjusted re-calculation and should not be interpreted as reproducing the sponsor's negative binomial model. The primary outcome has relatively large standard deviations in the arms, and recurrent events may be concentrated in some participants. Those features make the distinction between a simple count model and a model that accommodates over-dispersion particularly relevant. The sponsor's analysis takes precedence when its result differs from the recalculation.

What does the confidence interval add?

A confidence interval describes the range of estimates reasonably compatible with the observed data under the analysis model and its assumptions. For a rate ratio, an interval that includes 1 includes equal rates as one plausible value. A broad interval signals limited precision: the data do not pin down the comparative rate closely. An interval excluding 1 is often described as statistically inconsistent with equal rates under the model, but it does not by itself establish clinical importance. The sponsor's primary intervals include 1 for both dose comparisons.

How should p-values be read?

A p-value measures how unusual the observed data, or data more extreme, would be if the null hypothesis and the statistical model were correct. It is not the probability that the null hypothesis is true, nor is it the probability that the result occurred by chance. The sponsor reports p > 0.999 for each primary comparison. The registry record labels these analyses as superiority comparisons. The details of any multiplicity strategy or testing hierarchy are not reported in the registry record, so these p-values should not be read as resolving the broader set of outcome comparisons.

What do the group summaries describe?

The arm means are annualized rates, while the accompanying spread is the standard deviation. A standard deviation describes the spread of participant-level observations around a group mean; it is not the uncertainty around the mean and is not a confidence interval. The group sizes differ across the three arms, and the means and standard deviations alone do not capture participant-level event patterns. For example, they cannot show whether the event burden was broadly distributed or concentrated among a smaller number of participants.

What is the role of recalculation?

A recalculation from summary statistics is useful as a transparent numerical check, but it cannot account for unpublished analysis details or replace a model fit to participant-level data. It may differ from the sponsor's reported result because the approaches use different assumptions and methods. In this trial, the record explicitly indicates a discrepancy. The sponsor's reported negative binomial estimates, confidence intervals, and p-values are therefore the primary source for interpreting the registered analysis; the unadjusted recalculation is supplementary and should not override that analysis.

General statistical interpretation also depends on design and data-handling choices. Randomization supports a comparative analysis, but the validity and precision of a specific estimate still depend on how recurrent events, observation time, missing information, and changes in background therapies were handled. Those additional details are not reported in the registry record. They should not be inferred from the outcome definitions or from the posted summary statistics.

11. Confidence Intervals and Precision

The sponsor's 95% confidence interval for the 5.0 mg/kg comparison runs from 0.76 to 1.55 for the rate ratio. For 7.5 mg/kg, it runs from 0.62 to 1.27. Both intervals include 1, the equal-rate value, and each spans values on both sides of that point. The estimates are therefore not precise enough to distinguish a clear increase from a clear decrease in the comparative event rate under the sponsor's model.

Confidence intervals are more informative than a point estimate alone because they show uncertainty in the estimated comparison. A point estimate close to 1 does not prove that the rates are the same. Conversely, an estimate on one side of 1 does not establish a dependable difference when its interval also includes 1. The sponsor's intervals allow a range of comparative rate values, so the results are not tightly estimated.

The posted standard deviations are also substantial: 2.98 for the 5.0 mg/kg arm, 2.3 for the 7.5 mg/kg arm, and 2.81 for placebo. These values describe variation among observations, not uncertainty in the estimated rate ratios. The distinction matters: variability in participant outcomes and precision of a treatment comparison are related, but they are not interchangeable quantities.

General explanation: interval width is influenced by the amount of information in the data and by variability, as well as by the analysis model. The registry record does not report further details that would allow the sponsor's precision to be independently reconstructed from participant-level information. The separate unadjusted recalculation is not the sponsor's model and differs from the sponsor-reported results; the sponsor's own confidence intervals take precedence.

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 express sample size as participants per arm for 80% power and participants per arm for 90% power. They are not total event counts. The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each illustration considers detecting the stated fraction of the observed effect. For time-to-event planning estimates, the convention is total events using the Schoenfeld method; the comparisons discussed for these rate, continuous, and binary outcomes are expressed as participants per arm.

The 80% power column gives the number of participants per arm that the planning calculation estimates would be needed to have an 80% chance of detecting the specified effect under its assumptions, if that effect were the true effect. The 90% power column uses the same idea with a higher target chance of detection. Reaching a higher target power generally requires a larger planned sample. These are design illustrations based on an observed effect, not a reconstruction of the trial's original design assumptions; the trial's own sample-size justification is not reported in the registry record.

The rows for planning for 75% of the observed effect and 50% of the observed effect use smaller effects than planning for 100% of the observed effect. Smaller effects are harder to distinguish from random variation, so they require more participants per arm under the stated assumptions. The estimates can rise sharply when the effect to detect becomes smaller, particularly when the observed effect is itself small or imprecise.

These figures are not observed power. Observed power is not a useful substitute for reading the confidence interval and the uncertainty in the estimated effect after a trial. The planning illustrations are hypothetical scenarios to show how sample requirements change with the assumed effect and target power. They should not be interpreted as proof that the trial was adequately or inadequately designed.

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, λ₀ and λ₁ are event rates per patient-year, and T is follow-up per participant in years. This assumes Poisson counts and equal follow-up.

Worked calculation for this trial

1. Control rate λ₀ = 2.1000; treatment rate λ₁ = 2.5000 events per patient-year; follow-up T = 1.00 years.
2. n = (1.96 + 0.842)² × (1/2.1000 + 1/2.5000) / (1.00 × [ln(1.190)]²) = 226.2, rounded up to 227 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
lambda0 <- 2.1                      # control rate, events per patient-year
lambda1 <- 2.5                      # treatment rate
tt      <- 1                       # follow-up per participant, years
n_per_arm <- function(power, frac = 1) {
  l1 <- lambda0 * (lambda1 / lambda0)^frac   # smaller effect = fraction of the observed log rate ratio
  ceiling(round((z_a + qnorm(power))^2 * (1 / lambda0 + 1 / l1) / (tt * log(l1 / lambda0)^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 = ",")))

# Simulation 1: Poisson counts. Simulation 2: over-dispersed counts (variance = 1.5 x mean), analysed with the matching variance.
set.seed(3814746)
n    <- n_per_arm(0.80)
reps <- 20000
m0 <- lambda0 * n * tt; m1 <- lambda1 * n * tt
x0 <- rpois(reps, m0); x1 <- rpois(reps, m1)
z  <- log(x1 / x0) / sqrt(1 / x0 + 1 / x1)
cat(sprintf("Simulated power, Poisson counts, n = %s per arm: %.3f\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE)))
phi <- 1.5
y0 <- rnbinom(reps, mu = m0, size = m0 / (phi - 1)); y1 <- rnbinom(reps, mu = m1, size = m1 / (phi - 1))
z2 <- log(y1 / y0) / sqrt(phi * (1 / y0 + 1 / y1))
cat(sprintf("Simulated power, over-dispersed counts (phi = 1.5), same n: %.3f\n", mean(abs(z2) > z_a, na.rm = TRUE)))

Output from running the code

100% of observed effect: n per arm = 227 (80% power), 303 (90% power)
 75% of observed effect: n per arm = 411 (80% power), 550 (90% power)
 50% of observed effect: n per arm = 943 (80% power), 1,262 (90% power)
Simulated power, Poisson counts, n = 227 per arm: 0.800
Simulated power, over-dispersed counts (phi = 1.5), same n: 0.627

The first simulation draws Poisson counts and should land close to the target power. The second allows extra variability (variance 1.5 times the mean, a purely illustrative value), which lowers the power at the same sample size, so rate trials usually need more participants than the Poisson formula suggests.

14. Analyses Reported by the Sponsor

The registry reports the sponsor's primary comparisons from negative binomial regression: rate ratio 1.08, 95% confidence interval 0.76 to 1.55, and p > 0.999 for 5.0 mg/kg versus placebo; rate ratio 0.89, 95% confidence interval 0.62 to 1.27, and p > 0.999 for 7.5 mg/kg versus placebo. These are the trial's reported model-based results.

The unadjusted recalculation uses posted arm summaries and a simpler Poisson approach. The recalculated comparisons differ from the reported sponsor analyses. The registry record flags this discrepancy, so the sponsor's own analysis takes precedence. In particular, the recalculation should not be treated as a correction to the sponsor result or as an independent replication of the sponsor's model.

Differences can arise because a summary-statistic calculation cannot reproduce all features of a participant-level regression analysis, including any model specifications not reported in the registry record. The record does not give enough detail to identify the particular reason for the discrepancy. It is more appropriate to report both the distinction in methods and the sponsor's result than to speculate about the source of the difference.

The recalculated figures can serve as a rough, unadjusted check of the posted summaries, but they do not replace the sponsor's analysis for interpretation of the primary endpoint. Both approaches indicate substantial uncertainty rather than a precise comparative estimate. The reported sponsor intervals include the equal-rate value for both dose comparisons.

15. Multiplicity, Missing Data and Analysis Populations

The primary full analysis set is defined as all participants assigned study treatment by randomization. This identifies the intended population for the primary endpoint, but the registry record does not provide a fuller account of the analysis population for every secondary outcome. The outcome summaries also have varying arm counts: the primary endpoint uses 84, 83, and 85 participants, while some secondary summaries use smaller numbers. The reasons for those differences are not reported in the registry record.

Missing-data handling is not reported in the registry record. The record does not explain how missing endpoint observations, incomplete follow-up, treatment discontinuation, or other gaps in event ascertainment were handled statistically. The primary endpoint definition specifies limits on observation time, including a maximum of 365 days and stopping points related to treatment and other therapies, but that definition does not fully describe the statistical handling of incomplete data.

The multiplicity strategy is also not reported in the registry record. The study includes a primary endpoint and multiple secondary outcomes, and the registry lists 24 outcome measures and 16 analyses. Without a reported hierarchy, adjustment method, or other prespecified control of multiple testing, it is not possible to determine how the reported or recalculated secondary comparisons were intended to contribute to confirmatory inference.

The registry record does not report interim analyses, stopping rules, or the trial's original sample-size justification. It also does not report enough detail to assess whether covariates or stratification factors were included in the sponsor's regression model. These details should not be inferred from the trial's phase, randomization, or masking description.

These omissions limit independent assessment of the analysis plan and of how well each posted result corresponds to a prespecified test. They do not invalidate the posted outcomes automatically, but they make it important to distinguish the sponsor-reported primary analysis from unadjusted recalculations and exploratory secondary comparisons.

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 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: covid-19 (7.2%), pneumonia (7.1%), pulmonary embolism (4.8%), anaemia (3.6%), haemolysis (3.6%).

The registry reports on-treatment serious adverse event figures for 84 participants in the 5.0 mg/kg arm, 83 in the 7.5 mg/kg arm, and 85 in the placebo arm. Serious adverse events were recorded for 35, 22, and 26 participants, respectively. The record also lists 2 deaths in each arm. These are descriptive counts from the posted safety results; they do not establish that treatment caused an event or that groups differ in safety.

The most frequently listed serious adverse event terms include COVID-19 at 7.2%, pneumonia at 7.1%, pulmonary embolism at 4.8%, anaemia at 3.6%, haemolysis at 3.6%, and sepsis at 3.6%. The registry listing does not give an arm-specific breakdown for these terms in the information, so the percentages should not be attributed to any one treatment group.

Safety counts need interpretation in light of the number of participants observed, exposure time, event definitions, and clinical context. Further detail about event timing, severity beyond the serious classification, relationship to study treatment, or comparative statistical testing is not reported in the registry record. These figures describe recorded events; they do not provide individualized medical guidance.

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

The primary result addresses a specific statistical question: the comparative annualized rate of defined vaso-occlusive crisis events leading to a healthcare visit over a one-year timeframe. In the sponsor-reported analysis, the rate-ratio confidence intervals include 1 for both crizanlizumab doses versus placebo. The posted estimates are therefore uncertain and do not establish a clear difference on this endpoint.

This is not evidence that the doses and placebo are equivalent. A finding of equivalence would require an appropriate design, a prespecified equivalence margin, and an analysis designed to test that question. Those details are not reported in the registry record. Similarly, the results do not establish that one group had no crises: the outcome is a group event rate, and the arm summaries show observed events across the groups.

The endpoint does not encompass every aspect of sickle cell disease or every possible measure of patient experience. It focuses on crises meeting the registry's event definition and leading to healthcare visits. Other outcomes, such as crises treated at home, crisis duration, being free of a healthcare-visit crisis, and healthcare use, address different aspects of the condition. The available secondary data do not remove the uncertainty in the primary comparison.

Interpretation is also constrained by analysis details that are not reported, including missing-data methods, multiplicity handling, and parts of the sponsor's model specification. The unadjusted recalculation differs from the sponsor's result, and the sponsor's own analysis takes precedence. These limitations counsel against making a broader inference than the registered endpoint and posted analyses support.

In short, the posted primary results do not demonstrate a clear difference between either dose and placebo in the annualized rate of healthcare-visit vaso-occlusive crises. They also do not prove the absence of a difference, establish equivalence, or settle outcomes beyond the defined endpoint. Statistical uncertainty is a property of the evidence, not a verdict about an individual's treatment.

18. Why This Trial Matters Statistically

This trial illustrates why recurrent-event endpoints need careful statistical treatment. Counting crisis events per year retains information about repeated events and observation time, unlike an outcome that records only whether a participant experienced any event. At the same time, event rates can be highly variable across participants. The sponsor's use of negative binomial regression is relevant because that model can accommodate over-dispersion, whereas a simple Poisson recalculation relies on a more restrictive count-variation assumption.

It also demonstrates why the reported model and an unadjusted calculation from group summaries may not agree. The posted means and standard deviations are useful descriptions, but they cannot reproduce every aspect of participant-level analysis. When a discrepancy is explicitly recorded, the sponsor's reported analysis should be distinguished from the supplementary recalculation rather than blended with it.

The confidence intervals are central to interpretation. Point estimates alone might invite overconfident statements about which group had a higher or lower rate, while intervals that include the equal-rate value show that the comparisons remain uncertain. A non-significant result is not proof of no effect, just as a numerical trend is not proof of an effect.

Finally, the secondary outcomes and safety summaries show why a trial's evidence must be read across outcome definitions, populations, and analysis plans. Multiple outcomes can provide broader context, but their interpretation depends on prespecification, multiplicity handling, and complete reporting. Those parts of the statistical plan are not reported in the registry record. This makes transparent separation of primary, secondary, descriptive, and recalculated results especially important.

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.
• Rate comparisons use a Poisson approximation unless the sponsor posted confidence limits; real event counts are often over-dispersed.

The main trial-specific limitation is the discrepancy between the simple recalculations from posted summaries and the sponsor's reported negative binomial analyses. The registry record marks this discrepancy, and the sponsor's own analysis takes precedence. The posted record does not contain enough model detail to explain why the estimates differ, so no specific cause can be identified.

The event-rate endpoint depends on a defined observation window that can end before 365 days for reasons described in the registry. The record does not report how the sponsor handled incomplete observation, missing event information, or changes in background therapies in the analysis. Since this is a recurrent-event outcome, the distribution of events across participants may also matter, but participant-level data are not included in the posted summaries.

Some secondary outcomes have smaller analysis counts than the primary endpoint. The reasons for the differences are not reported in the registry record. The secondary endpoints also include different kinds of outcomes, and the record does not describe a complete multiplicity strategy. This makes isolated secondary comparisons less reliable as confirmatory claims.

The registry reports the primary outcome and several secondary summaries, but it does not report the original sample-size justification, full statistical analysis plan, interim-analysis procedures, or all model specifications. As a result, it is not possible to assess the original design assumptions or independently reproduce the sponsor's analyses from the summaries alone.

These limitations affect precision and independent interpretation, but they should not be confused with evidence that a particular result is wrong. The appropriate response is to keep conclusions close to the reported analyses, distinguish sponsor results from recalculations, and avoid claims that depend on unreported methods.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Study of Two Doses of Crizanlizumab Versus Placebo in Adolescent and Adult Sickle Cell Disease Patients — NCT03814746.
• Registry record last updated 2026-10-14; status last verified 2026-09.
• Results first posted 2024-01-08.
• 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

The registry record describes STAND, a phase III randomized, multicenter study of crizanlizumab at 5.0 mg/kg or 7.5 mg/kg versus placebo in adolescent and adult patients with sickle cell disease and a history of healthcare-visit vaso-occlusive crises. The primary endpoint was the annualized rate of healthcare-visit crises over one year.

The sponsor-reported negative binomial comparisons gave rate ratios of 1.08 and 0.89, with 95% confidence intervals of 0.76 to 1.55 and 0.62 to 1.27, respectively; both reported p-values were > 0.999. Both intervals include 1, leaving the primary comparisons uncertain. A simple unadjusted recalculation differs, and the sponsor's analysis takes precedence.

Important analysis details, including the multiplicity strategy, missing-data methods, and original sample-size justification, are not reported in the registry record. The posted secondary outcomes and safety counts add context but do not resolve the uncertainty in the primary result.