A Study of Prasugrel in Pediatric Participants With Sickle Cell Disease (SCD): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study of Prasugrel in Pediatric Participants With Sickle Cell Disease (SCD) (NCT01794000), a randomized phase 3 study. The primary outcome is Number of Vaso-Occlusive Crisis (VOC) Events Per Participant Per Year (Rate of VOC).

2. Clinical Question

The study’s stated purpose was to evaluate prasugrel’s efficacy and safety in reducing vaso-occlusive crisis events in children with sickle cell disease. It also investigated daily pain. The primary endpoint combines painful crisis and acute chest syndrome, so the question concerns the rate of a composite of clinically relevant crisis events rather than a single event type. Events within 7 days of the prior event’s onset were not counted as a new episode.

The registry describes random assignment to prasugrel or placebo and identifies the primary outcome population as all randomized participants. It lists follow-up from randomization through 24 Months. The record also lists pain-related measures and other sickle-cell-related events as secondary outcomes. Those measures address different aspects of illness experience and healthcare use, but they do not replace the primary event-rate question.

The question is about a group-level comparison of event rates over exposure time. It does not ask whether every participant had an event, nor does the rate alone describe how events were distributed among participants. The posted summary does not report participant-level event patterns, so the primary comparison should be read as an average rate comparison rather than a description of individual courses.

3. Trial Design

The registry identifies this as a phase 3, randomized, triple-masked, parallel-group comparison of prasugrel and placebo in pediatric participants with sickle cell disease. The listed enrollment is 341. The two registered groups are Prasugrel and Placebo. The active-treatment description says participants were titrated from an initial daily oral dose toward a specified P2Y12 reaction-unit range; the placebo group received daily oral placebo and followed an identical visit schedule.

The study start is recorded as 2013-04, and primary completion as 2015-07. Its status is TERMINATED. The registry record does not report why the study was terminated, so the status alone does not establish whether termination was planned, related to efficacy or safety, or due to another reason. The record does not report the trial’s original sample-size justification or the design assumptions used for that justification.

The primary endpoint covers randomization through 24 Months, and the outcome description says data were collected through the stated primary completion date. The primary population is all randomized participants. Group summaries list 171.0 participants for prasugrel and 170.0 for placebo. These are the displayed group sizes; the posted record does not provide further detail about inclusion in each endpoint analysis or how incomplete follow-up was handled.

The registry lists 13 outcome measures and 13 analyses, including the primary endpoint and pain, crisis, hospitalization, acute chest syndrome, transfusion, analgesic-use, and school-absence outcomes. It lists 12 posted secondary outcomes. The detailed protocol, the precise masking procedures, the allocation-concealment process, and the analysis plan are not reported in the registry record.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Double-Blind Phase (DBP)

Reasons for not completing this period:

Open-Label Extension Phase (OLE)

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: All randomized participants.

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: All randomized participants.

6. Primary Endpoint

The registry lists the primary outcome as Number of Vaso-Occlusive Crisis (VOC) Events Per Participant Per Year (Rate of VOC), measured over Randomization through 24 Months.

The primary endpoint is the number of vaso-occlusive crisis events per participant-year from randomization through 24 Months. The registry defines a vaso-occlusive crisis as a composite of painful crisis or acute chest syndrome. A repeat event was not counted when it occurred within 7 days from the prior event’s onset date. The outcome is expressed as an event rate, so it relates the number of qualifying events to participant-time rather than reporting only whether a participant experienced any event.

Using a rate is useful when participants can experience recurrent events and may contribute different amounts of observation time. It allows the comparison to reflect both event counts and time under observation. A rate ratio then compares the event rate in one group with that in the other. A value below 1 indicates a lower estimated rate in the prasugrel group relative to placebo; it does not by itself say how many participants avoided an event or how events were distributed among individuals.

The composite endpoint captures two event categories, but a combined rate can conceal differences between its components. The primary summary does not separately show the contribution of painful crisis and acute chest syndrome to the overall comparison. Nor does it report each participant’s total follow-up or recurrent-event pattern. Those details are not reported in the registry record. The endpoint therefore gives a concise summary of recurrent crisis-event frequency over exposure time, while leaving the component-specific and participant-level experience unresolved.

7. Results Posted in the Registry

• Prasugrel: 2.29 versus 2.77 (Number of Events per Participant-Year) on control; rate ratio 0.83 (95% CI 0.75–0.91, approximate, Poisson model); p ≈ <0.001.

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.

Monthly Rate of Days With Pain

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard errors.
• Result:
  • Prasugrel: mean 17.46 versus 17.70 on control; difference -0.24 (95% CI -4.55 to 4.07), standardized effect d = -0.01; z-test p = 0.912.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Prasugrel and the control. The interval gives the range of effects that remain compatible with the data.

Monthly Mean in Faces Pain Scale-Revised Score

• 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 errors.
• Result:
  • Prasugrel: mean 0.71 versus 0.61 on control; difference 0.10 (95% CI -0.11 to 0.31), standardized effect d = 0.11; z-test p = 0.365.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Prasugrel and the control. The interval gives the range of effects that remain compatible with the data.

Number of Painful Crisis Events Per Participant Per Year (Rate of Painful Crisis)

• 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:
  • Prasugrel: 2.24 versus 2.72 (Number of Events per Participant-Year) on control; rate ratio 0.82 (95% CI 0.75–0.91, approximate, Poisson model); p ≈ <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference (a ratio of 1), so the event rate is statistically lower for Prasugrel than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes span pain frequency and intensity, painful crisis events, hospitalizations for vaso-occlusive crisis, acute chest syndrome, red blood cell transfusions, analgesic use, and school absence due to sickle cell pain. The broad pattern is mixed in terms of certainty: the simple recalculations for the two event-rate outcomes point in the same direction as the primary rate comparison, while the posted pain measures do not show a clear separation in their reported model-based comparisons. The sponsor-reported event-rate analyses are less conclusive than the corresponding simple recalculations.

These outcomes are related to the primary question but are not interchangeable with it. Pain days and pain scale scores describe aspects of pain experience; hospitalization, acute chest syndrome, transfusion, and school absence reflect other consequences or care-related events. Agreement across related measures could add context, while disagreement may reflect different constructs, follow-up, variability, or analysis methods. The registry summaries do not establish which explanation accounts for any pattern.

The secondary findings do not overturn or resolve the primary discrepancy. The primary endpoint remains the designated composite crisis-event rate, and the sponsor’s analysis of that endpoint remains the key result. Secondary estimates can help describe the wider outcome profile, but they should not be treated as independent confirmation of a primary conclusion, especially when some estimates are imprecise or based on different models.

Unadjusted secondary results carry less weight because multiple outcomes create multiple opportunities for apparently notable findings by chance. The registry record does not report a multiplicity strategy or a hierarchy governing interpretation of secondary outcomes. Without that information, individual secondary p-values should be regarded as descriptive or exploratory rather than as definitive evidence. The record also does not provide a complete account of which secondary analyses were prespecified, so their confirmatory status cannot be determined from the registry entry alone.

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

• Monthly Rate of Days With Pain
• Monthly Mean in Faces Pain Scale-Revised Score
• Number of Painful Crisis Events Per Participant Per Year (Rate of Painful Crisis)
• Number of Hospitalizations for VOC Per Participant Per Year (Rate of Hospitalizations)
• Number of Acute Chest Syndrome Per Participant Per Year (Rate of Acute Chest Syndrome)
• Number of Red Blood Cell (RBC) Transfusions Due to Sickle Cell Disease (SCD) Per Participant Per Year (Rate of RBC Transfusions)
• Monthly Rate of Days of Analgesic Use
• Quarterly Rate of School Absence Due to Sickle Cell Pain

9. Statistical Interpretation

10. Statistical Methods Explained

The central statistical feature is that the primary outcome counts recurrent events over participant-time. A participant may contribute more than one qualifying event, unlike a simple binary outcome that records only whether an event occurred. Dividing the event count by time at risk produces a rate, and comparing rates with a rate ratio expresses the relative event frequency between groups. General interpretation: a rate ratio of 1 represents equal rates, while a value below 1 represents a lower rate in the numerator group. It is not an absolute difference in event counts.

Why compare event rates?

Participant-time rates can be useful when follow-up duration differs or when recurrent events are part of the question. The primary endpoint is reported per participant-year, and the follow-up timeframe is listed as randomization through 24 Months. The registry summary gives rates for each arm and a rate ratio. The record does not give the individual exposure times or a detailed account of how censoring and incomplete observations entered the sponsor’s model. Those details should not be inferred from the rate summaries alone.

A simple Poisson-style rate comparison treats event counts in relation to exposure time under a specified count model. General explanation: such models commonly rely on assumptions about how the event counts vary around their expected rates. If variation is greater than the model allows, a phenomenon called over-dispersion, standard errors can be too small and confidence intervals too narrow. Repeated events may also be correlated within a participant. A simple recalculation from aggregate counts cannot fully represent participant-level dependence or every feature of a recurrent-event analysis.

What does the sponsor’s model add?

The reported primary analysis uses an Andersen-Gill model and reports a rate ratio with a confidence interval and p-value. This is a recurrent-event modeling approach. The registry record does not report the full model specification, covariates, variance estimator, or handling of event dependence. It is therefore not possible to reconstruct the sponsor’s analysis from the displayed arm-level rates alone. The sponsor-reported estimate and uncertainty are the appropriate primary analysis to cite, particularly because they differ from the summary-based recalculation.

The recalculated estimate is an unadjusted comparison derived from the posted rate summaries and event information. It offers a transparent check on the direction and rough scale of the posted data, but it is not a substitute for an analysis using participant-level records and the sponsor’s model. Its confidence interval and p-value should be understood as belonging to that recalculation, not as an alternative official trial result. Given the discrepancy, the sponsor’s own analysis takes precedence.

How should the confidence interval and p-value be read?

A confidence interval describes the range of values compatible with the estimate under the analysis and its assumptions, with a stated long-run coverage interpretation. It communicates uncertainty as well as direction. For a rate ratio, an interval containing 1 includes equal rates among the values compatible with the model; an interval excluding 1 indicates that equal rates are not within that interval. The sponsor’s primary interval includes 1, whereas the recalculated interval does not. This contrast is central to interpreting the result.

A p-value describes how unusual data at least as discrepant as those observed would be under a specified null hypothesis and statistical model. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of an effect. The sponsor’s p-value and the recalculated p-value arise from different analyses, so they should not be treated as interchangeable measures of the same calculation. The registry record does not state a multiplicity adjustment for the reported outcomes.

What do the continuous secondary analyses estimate?

The posted pain outcomes include least-squares means and mean differences. A least-squares mean is a model-based group mean, and a mean difference contrasts the modeled means. The registry reports mixed models analyses for these outcomes. The exact model specification and covariance assumptions are not reported in the registry record. The recalculations for continuous outcomes use the posted means and standard errors to form approximate unadjusted comparisons; they do not reproduce the mixed models analyses.

General explanation: standard errors quantify uncertainty in an estimated quantity, while standard deviations describe variation among observations. Confusing them can lead to misreading the precision of a mean. For the posted pain outcomes, the registry labels the displayed dispersion as standard error. Any conversion used for a recalculation is approximate and is not a replacement for the original model. The sponsor’s reported mixed-model estimates remain the source for the official analyses.

Why does model choice matter?

Different methods can use information differently and can produce different estimates of uncertainty, especially for repeated events, unequal observation, and correlated outcomes. A simple rate calculation may summarize totals effectively, but it cannot capture all participant-level structure. A recurrent-event model can address features of event timing and recurrence within its specified framework, though its conclusions still depend on the model and its assumptions. Because the registry does not report the complete protocol or model details, the available record supports describing the analyses and their disagreement, not deciding which unreported modeling choice caused it.

11. Confidence Intervals and Precision

The sponsor’s primary estimate is a rate ratio of 0.83, with a 95% confidence interval from 0.66 to 1.05. The point estimate is below 1, but the interval includes 1 and extends to values compatible with a higher rate in the prasugrel group relative to placebo. Thus, the sponsor’s reported result leaves uncertainty about whether the underlying rates differ and, if so, in which direction. The p-value is .117, consistent with that uncertainty under the reported model.

The recalculation from posted summaries gives a narrower interval, from 0.754 to 0.912, around a rate ratio of 0.829. That calculation suggests more precision than the sponsor-reported analysis. Because the results differ, the narrower interval should not be used to replace the sponsor’s interval. The sponsor’s own analysis takes precedence, and the contrast itself is relevant when judging how much certainty the registry results support.

In general, a confidence interval is not a range that contains the true effect with a probability attached after observing the data. It is produced by a method that, over repeated studies under its assumptions, has the stated coverage. Its width reflects both the information in the data and the analysis assumptions. A relatively narrow interval can still be misleading if the model does not adequately represent the data structure; a wider interval communicates greater uncertainty but does not identify its cause.

Precision is also limited by what the summary leaves out. The registry record does not report participant-level event distributions, model diagnostics, or the details needed to independently reproduce the sponsor’s estimate. A composite endpoint further limits precision about each component because the displayed primary estimate combines painful crisis and acute chest syndrome. The primary result is therefore best read with attention to its model-based interval and the discrepancy with the recalculation, rather than relying on the point estimate alone.

12. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The planning figures are illustrative calculations based on the observed effect, not the trial’s original design justification. For these rate outcomes, the figures are participants per arm, rather than a total event count. The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation; each scenario uses the stated fraction of the observed effect. The registry record does not report the assumptions used for the original trial design.

The 80% power column gives the illustrated participants per arm for a design with an 80% chance of detecting the chosen effect under those assumptions, if that effect were the true one. The 90% power column gives the corresponding planning figure for a design with a 90% chance. These are prospective design concepts, not measures of how likely the completed trial was to find a result after its data were observed. The calculations are planning illustrations and are not observed power.

Rows describe planning for 100%, 75%, and 50% of the observed effect. Smaller effects are harder to distinguish from random variation, so detecting them generally requires more participants. This pattern is reflected in the displayed planning figures. The same assumptions govern the curve: it is another representation of the planning relationship, not evidence that the trial enrolled enough participants or that a particular effect was established.

The illustrations do not account for every possible feature of the actual trial or analysis. In particular, the registry does not report that these planning calculations were used in trial design. They should not be interpreted as proof that the trial had a specified probability of detecting the sponsor’s modeled effect. Their role is to show how the required planning scale changes when the target effect is set to different fractions of the observed estimate.

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 = 2.7670; treatment rate λ₁ = 2.2950 events per patient-year; follow-up T = 2.00 years.
2. n = (1.96 + 0.842)² × (1/2.7670 + 1/2.2950) / (2.00 × [ln(0.829)]²) = 89.4, rounded up to 90 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 <- 2.767                      # control rate, events per patient-year
lambda1 <- 2.295                      # treatment rate
tt      <- 2                       # 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(1794000)
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 = 90 (80% power), 120 (90% power)
 75% of observed effect: n per arm = 156 (80% power), 208 (90% power)
 50% of observed effect: n per arm = 341 (80% power), 456 (90% power)
Simulated power, Poisson counts, n = 90 per arm: 0.806
Simulated power, over-dispersed counts (phi = 1.5), same n: 0.630

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 sponsor’s reported primary analysis uses an Andersen-Gill model and gives a rate ratio of 0.83, with a 95% confidence interval from 0.66 to 1.05 and p = .117. The recalculation from posted summary counts gives a rate ratio of 0.829, with a 95% confidence interval from 0.754 to 0.912 and p < 0.001. The point estimates are similar, but the intervals and p-values differ materially. Similar point estimates do not mean that the analyses provide the same certainty.

The recalculation is a simple, unadjusted calculation from posted summary statistics; it is not a reproduction of the participant-level Andersen-Gill analysis. Recurrent-event structure and model-based uncertainty can affect the interval and test. The registry does not report enough of the sponsor’s model specification to identify the source of the difference. As a result, the recalculation is useful as a check on the posted summaries but should not be used to overrule the reported analysis.

The sponsor’s own analysis takes precedence when describing the trial’s primary result. Its interval includes 1, and its reported p-value does not establish a clear difference under that analysis. The discrepancy should remain visible in any interpretation: the recalculated summaries look more conclusive than the sponsor’s model, but the official result is the sponsor-reported estimate and its uncertainty.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists 13 outcome measures and 13 analyses, including the primary endpoint, and 12 secondary outcomes are posted. Evaluating multiple outcomes can increase the chance that at least one result appears notable even when there is no corresponding underlying effect. Statistical approaches such as prespecified outcome hierarchies or adjustments can address some of this issue, but the registry record does not report whether any such strategy was used. It also does not report a multiplicity-adjusted analysis for the posted secondary results.

The record identifies the primary endpoint and names the secondary measures, but does not provide enough information to determine how the investigators planned to control the overall type I error, whether secondary analyses were confirmatory, or how testing was sequenced. The p-values in the posted results should therefore be read as analysis-specific rather than as evidence that the full family of outcomes was controlled for multiplicity. This is especially relevant when interpreting a collection of secondary results or emphasizing an isolated finding.

Missing-data handling is also not reported in the registry record. The primary population is described as all randomized participants, but that description does not establish how missing endpoint observations, incomplete follow-up, discontinuation, or missed visits were handled in the analysis. The displayed primary group sizes and the smaller displayed counts for some secondary outcomes do not, by themselves, explain why observations were unavailable or whether the analysis used imputation, likelihood methods, or another approach.

The primary analysis population is stated as all randomized participants, which identifies the intended population for that endpoint. The record does not explain whether every randomized participant contributed usable primary endpoint data, nor does it report sensitivity analyses addressing missing outcomes. Interim analyses, stopping rules, and the trial’s detailed statistical analysis plan are not reported in the registry record. These omissions limit assessment of how robust the posted estimates are to analytic choices, but they do not justify assuming that a particular method was or was not used.

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 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: sickle cell anaemia with crisis (48.8%), anaemia (11.8%), acute chest syndrome (8.8%), malaria (6.5%), pneumonia (4.1%).

For the double-blind phase, the adverse-event summary lists 170 participants at risk in each group. Serious adverse events affected 100 participants in the prasugrel group and 106 in the placebo group. Other adverse events affected 148 participants in the prasugrel group and 154 in the placebo group. These are descriptive group counts; they do not by themselves establish that treatment caused or prevented any event. The registry does not provide a comparative statistical analysis for these summaries in the information.

The listed serious adverse-event terms include sickle cell anaemia with crisis (48.8%), anaemia (11.8%), acute chest syndrome (8.8%), malaria (6.5%), pneumonia (4.1%), and Plasmodium falciparum infection (3.5%). These percentages are reported terms, not a full account of severity, timing, recurrence, or attribution. The record also lists an open-label prasugrel phase with 3 participants at risk, 0 affected by serious adverse events, and 1 affected by other adverse events. Death counts are not reported in the registry record.

Safety summaries should be interpreted in light of the groups and phases to which they apply. The open-label group is not a randomized comparison equivalent to the double-blind groups. The record does not report detailed exposure-adjusted safety rates or sufficient information to compare risk while accounting for follow-up duration. Counts alone are therefore useful for describing what was recorded, not for making causal or clinical conclusions.

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

The primary result describes an estimated rate of a defined composite of painful crisis and acute chest syndrome, counted under the registry’s episode rule and expressed per participant-year. The sponsor’s model estimates a rate ratio below 1, but its confidence interval includes 1. That means the posted sponsor analysis does not pin down a clear difference between groups with high precision. The point estimate is not a guarantee of the true effect, and the interval permits a range of effects that includes equal rates.

The summary-based recalculation appears more conclusive, but it uses a simpler method and differs from the sponsor’s reported recurrent-event analysis. The sponsor’s own analysis takes precedence. The discrepancy means the recalculation should be presented as a sensitivity-like descriptive check, not as the definitive trial conclusion or as proof that the sponsor analysis is wrong.

Neither the primary rate nor the secondary outcomes establish what an individual participant should expect. A group average can coexist with variation in participant experience, and the posted summaries do not describe individual event trajectories. The composite result also does not show the separate effects on painful crisis and acute chest syndrome. The registry does not report enough information to draw conclusions about those components independently.

The findings also do not settle every question about pain, healthcare use, or safety. Secondary outcomes measure different dimensions and are subject to uncertainty and multiplicity concerns. Safety counts are descriptive and do not establish causation. The registry status is TERMINATED, but the reason for termination is not reported, so no conclusion about the reason or its relationship to the results is warranted.

In short, the record documents a randomized comparison and a sponsor-reported primary rate ratio whose uncertainty includes no difference. It also contains a simpler recalculation with narrower uncertainty. Reading the sponsor analysis as primary, while acknowledging that discrepancy and the limitations of the posted summaries, is the most faithful statistical interpretation of the record.

18. Why This Trial Matters Statistically

This trial raises a central issue in clinical biostatistics: the distinction between a summary-level recalculation and the prespecified or sponsor-reported model for recurrent events. When participants can experience repeated events, treating the data as simple aggregate counts may produce uncertainty estimates that differ from a model using event-level information and its assumptions. Here, the point estimates are close, yet the uncertainty and inferential conclusions differ. That contrast shows why the analysis method is part of the result rather than a technical afterthought.

It also illustrates the importance of separating effect direction from precision. A rate ratio below 1 is a directional estimate, but confidence intervals describe how much uncertainty remains. The sponsor’s interval includes equal rates, whereas the recalculated interval does not. A reader who focuses only on the point estimate could miss this distinction; a reader who focuses only on one p-value could miss the model discrepancy.

The endpoint’s recurrent-event structure and composite definition matter as well. Rates account for exposure time and repeated crises, while the composite combines painful crisis with acute chest syndrome. Those choices shape the scientific question answered by the analysis. Component-level results and participant-level event distributions would provide additional context, but they are not reported in the registry record.

Finally, the trial record demonstrates why a complete statistical plan matters for interpretation. Details about multiplicity, missing data, model specification, and the original design assumptions are not reported. Without those details, the secondary outcomes and planning illustrations must be read cautiously. The registry still permits a clear account of the reported design and results, but it does not support filling in unreported analytic decisions.

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 principal limitation for interpreting the primary comparison is the discrepancy between the summary-based recalculation and the sponsor’s Andersen-Gill analysis. The sponsor’s interval is wider and includes 1, while the recalculated interval does not. The registry record does not provide the complete model specification or participant-level data needed to explain the difference. The recalculation should therefore remain secondary to the sponsor-reported result.

The primary endpoint is a composite, and component-specific results are not reported. The event rule also excludes a new episode when its onset occurs within 7 days of the prior event’s onset. These features define what is counted but may make the endpoint less informative about the separate patterns of painful crisis and acute chest syndrome. Individual event distributions and follow-up contributions are not reported.

The trial status is TERMINATED, but the reason for termination is not reported in the registry record. The original sample-size justification, interim analyses, stopping rules, and full statistical analysis plan are also not reported. The planning illustrations based on observed effects cannot fill those gaps or establish what assumptions shaped the trial’s design.

Missing-data methods and sensitivity analyses are not reported. The record identifies all randomized participants as the primary outcome population, but does not explain how unavailable observations or incomplete follow-up were handled. Multiplicity procedures for the many outcomes are also not reported, limiting confirmatory interpretation of secondary p-values. Finally, safety results are posted as counts and selected terms without a detailed comparative analysis, exposure-adjusted rates, or reported death counts. These limitations constrain interpretation of the registry summaries; they do not establish that a particular bias or analytic problem occurred.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Study of Prasugrel in Pediatric Participants With Sickle Cell Disease (SCD) — NCT01794000.
• Registry record last updated 2019-09-25; status last verified 2019-09.
• Results first posted 2016-07-27.
• 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 describes a phase 3, randomized, triple-masked, parallel-group comparison of prasugrel and placebo in pediatric participants with sickle cell disease. Listed enrollment is 341, and the study status is TERMINATED. The primary endpoint is the rate of vaso-occlusive crisis events per participant-year from randomization through 24 Months, with painful crisis and acute chest syndrome included in the composite.

The sponsor-reported Andersen-Gill analysis gives a rate ratio of 0.83, a 95% confidence interval from 0.66 to 1.05, and p = .117. A simple recalculation from posted summaries is more conclusive, but the sponsor’s own analysis takes precedence. The registry also lists pain and other disease-related secondary outcomes, while multiplicity and missing-data methods are not reported.

The record supports describing the randomized design, endpoint definition, posted estimates, and their uncertainty. It does not report the reason for termination, the full analysis plan, or enough detail to resolve the discrepancy between the primary analyses.