A Phase II Trial of Regadenoson in Sickle Cell Anemia: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Phase II Trial of Regadenoson in Sickle Cell Anemia (NCT01788631), a randomized phase 2 study. The primary outcome is Number of Participants With a Reduction in Invariant Natural-Killer T-Cell (iNKT Cell) Activation by 70% or More.

2. Clinical Question

The question is framed around a short-term biological measure during a 48-hour infusion. The endpoint counts participants meeting a specified reduction threshold; it is not a continuous measure of the amount of change in every participant. The posted comparison therefore describes how many participants in each arm crossed that threshold, rather than the average change in iNKT-cell activation.

The registry record also lists secondary outcomes, including hospital stay, respiratory symptoms, opioid use, and inflammatory markers. These address other clinical or biological observations, but they are distinct from the primary question. Their presence in the record does not mean that all their results or statistical comparisons are posted.

3. Trial Design

The registry describes a Phase II, randomized, placebo-controlled trial with a parallel-group model and triple masking. The listed interventions were regadenoson and placebo. The study status is completed, and the listed enrollment is 100. Dana-Farber Cancer Institute is the sponsor. The record lists a start date of 2013-07 and a primary completion date of 2016-11-10.

The regadenoson arm is described as receiving 1.44 mcg/kg/hour infused over 48 hours; the placebo arm received placebo over 48 hours. The record does not report additional dosing details, adherence information, or the exact procedures used to implement masking. It also does not report the randomization method or allocation concealment procedures. Those design details should not be inferred from the fact that the trial was randomized and triple masked.

The primary outcome is reported for treated patients with baseline and end-of-infusion blood samples. The posted endpoint counts are 21 of 49 in the regadenoson arm and 10 of 43 in the placebo arm. These endpoint denominators are not the same as the adverse-event populations at risk, which are reported separately. The registry record does not explain the relationship between enrollment, allocation, treatment, and the endpoint-specific analysis population in enough detail to reconstruct participant flow.

Although the title and design identify the study as Phase II, the registry record does not report the trial’s original sample-size justification or the assumptions used to design the trial. The separate planning illustrations are calculations based on the observed effect, not the original design plan. The record also does not report the original statistical analysis plan, the timing of any interim analyses, or detailed procedures for handling missing observations.

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: Prior to study arm randomization and assignment, patients were screened using the following testing methods: Confirmation of sickle cell genotype, complete blood count with differential, chemistry, coagulation testing (Including PTT, and INR), and pregnancy testing for female participants.

Overall Study

Analysis population for the primary outcome, as defined in the registry: Treated patients with baseline and end of infusion blood samples.

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 enrolled patients.

6. Primary Endpoint

The registry lists the primary outcome as Number of Participants With a Reduction in Invariant Natural-Killer T-Cell (iNKT Cell) Activation by 70% or More, measured over Baseline-End of study infusion over 48 hours.

The primary endpoint counts participants whose iNKT-cell activation fell by 70% or more between baseline and the end of the 48-hour study infusion. The registry describes the purpose as determining whether infusional regadenoson reduced iNKT-cell activation among individuals with sickle cell anemia and pain or acute chest syndrome, compared with placebo. The stated analysis population is treated patients with both baseline and end-of-infusion blood samples.

This is a binary endpoint: each participant is counted as either meeting the reduction threshold or not meeting it. A threshold-based endpoint can make a biological change easier to summarize as a group comparison, but it also discards information about how far participants above or below the threshold changed. Two participants with different amounts of reduction can contribute the same endpoint count if both meet the threshold.

The measure is a biological outcome observed over the infusion period. It is not itself a measure of length of hospital stay, pain relief, or another clinical benefit. The registry record does not report why the 70% threshold was selected, whether it was established before the trial, or how the laboratory measurement and threshold classification were validated. Those details should not be assumed when interpreting the count.

7. Results Posted in the Registry

• Regadenoson Arm: 42.9% (21/49) versus 23.3% (10/43) on control; risk difference 19.6 percentage points (95% CI 0.9 to 38.3), risk ratio 1.84 (0.98–3.47); unadjusted two-proportion z-test p = 0.047.

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.

Number of Participants With an Improvement in Respiratory Symptoms

• 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:
  • Regadenoson Arm: 20.4% (10/49) versus 20.9% (9/43) on control; risk difference -0.5 percentage points (95% CI -17.1 to 16.1), risk ratio 0.98 (0.44–2.17); unadjusted two-proportion z-test p = 0.951.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Regadenoson Arm and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists secondary outcomes spanning hospital stay, respiratory symptoms, opioid use, and inflammatory markers. Together, these outcomes address a broader set of clinical and biological observations than the primary iNKT-cell threshold. The posted results do not provide a complete numerical picture across that list: the respiratory-symptom outcome has a displayed comparison, while numerical results for the other listed outcomes are not reported in the registry record.

The respiratory-symptom comparison shows little separation between the observed arm proportions, and its interval spans contrasts in both directions. This pattern is not the same as the primary endpoint’s positive observed difference. The outcomes also measure different things, so agreement or disagreement between them would not be a direct validation of the primary endpoint. A biological threshold and a symptom outcome need not move together, and the registry record does not report a planned relationship between them.

Secondary outcomes are often useful for describing a trial’s broader measurements, but their results require cautious interpretation when many outcomes are considered. If many comparisons are examined, some may appear notable by chance even when there is no underlying difference. Whether the trial used a multiplicity adjustment, a hierarchical testing plan, or another strategy is not reported in the registry record. The displayed secondary comparison is unadjusted, so it carries less weight as confirmatory evidence than a result interpreted within a prespecified testing strategy.

The absence of reported numerical results for several listed outcomes should not be read as a null result or as evidence of no effect. It means that the registry record does not contain the estimates needed to assess their direction or precision. The secondary outcomes can help frame the scope of the trial, but they do not change what the primary comparison directly measures.

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

• Length of Hospital Stay
• Number of Participants With an Improvement in Respiratory Symptoms
• Opioid Use
• Level of Inflammatory Markers (A2A)
• Level of Inflammatory Markers (IL-4)
• Level of Inflammatory Markers (IFN-gamma)

9. Statistical Interpretation

10. Statistical Methods Explained

The endpoint is binary because each participant either met the stated 70% reduction threshold or did not. The basic summaries are counts and denominators, followed by proportions for the two arms. The comparison summary presents a risk difference, along with risk-ratio and odds-ratio measures. The record does not identify the exact inferential test or model used for the sponsor’s primary analysis, so the displayed statistics should not be attributed to a particular test without further documentation.

What does the risk difference express?

In general, a risk difference subtracts the event proportion in one group from the event proportion in the other group. Here, the event is meeting the iNKT-cell reduction threshold. A positive estimate indicates a larger observed proportion in the regadenoson arm, using the comparison direction shown in the posted summary. The estimate is 0.196. The risk difference is an absolute contrast on the proportion scale; it is not a percentage-point change unless expressed in that form, and no additional conversion is needed to interpret the reported value.

How do relative measures differ?

In general, a risk ratio compares the event proportions as a ratio, while an odds ratio compares the odds of the event. These measures answer different descriptive questions from the risk difference, and their numerical scales are not interchangeable. The comparison summary includes a risk ratio of 1.843 with an interval from 0.980 to 3.467, and an odds ratio of 2.475 with an interval from 1.0 to 6.124. Their intervals are important: both summaries remain imprecise, and neither should be interpreted without attending to the endpoint counts and uncertainty.

For binary outcomes, relative measures can appear more or less striking depending on the baseline event proportion, whereas the risk difference directly describes the absolute contrast between proportions. The registry record does not state which measure was designated as the primary effect measure in the original analysis plan. The posted risk difference is useful for describing the absolute contrast, but it does not replace the counts or resolve questions about study conduct and analysis.

What does the p-value say?

In general, a p-value describes how incompatible the observed data are with a specified null model, under the assumptions of the test used. It is not the probability that the null hypothesis is true, and it does not measure the magnitude or clinical importance of an effect. The primary comparison reports an unadjusted p-value of 0.047. The exact test and its assumptions are not reported in the registry record, and the result is not adjusted for multiple outcomes. It should therefore be read as a nominal comparison rather than as a complete account of the evidence across the trial.

The confidence interval provides a range of effect values compatible with the data under the interval procedure. In general, a wider interval signals less precision, while a narrower interval signals greater precision. The interval for the primary risk difference ranges from 0.009 to 0.384. Its lower endpoint is close to zero, while its upper endpoint allows a substantially larger positive difference. This spread illustrates why the point estimate alone gives an incomplete account of uncertainty.

What is recalculated, and what is not?

The simple comparisons in the posted summary are unadjusted comparisons based on the arm-level counts. They do not account for other variables or demonstrate an adjusted causal effect. The registry record reports no detailed adjustment strategy, covariate set, model diagnostics, or prespecified analysis plan. There are no reported analyses listed for the secondary outcomes in the registry record, apart from the displayed respiratory-symptom comparison.

In general, an adjusted analysis can account for measured covariates according to a specified model, while an unadjusted comparison uses the group summaries without such adjustment. Whether adjustment was planned or appropriate is not reported in the registry record. The counts and comparison should consequently be interpreted as the posted group-level evidence, not as a reconstruction of undocumented analyses.

Why does the endpoint population matter?

The primary endpoint description limits the population to treated participants with baseline and end-of-infusion blood samples. This means the posted endpoint comparison is not explicitly described as an intention-to-treat analysis of everyone randomized. The record does not report the number randomized to each arm, the reasons for missing endpoint measurements, or the rule used to include participants without both samples. These omissions limit assessment of whether endpoint availability could affect the comparison.

General statistical interpretation also depends on how the threshold was defined, how measurements were made, and whether analysis decisions were established before reviewing the results. Those details are not reported in the registry record. No assumptions about them should be substituted for documentation. The statistical summary is informative as a description of the posted endpoint counts and contrasts, while the missing analysis details constrain stronger conclusions.

11. Confidence Intervals and Precision

The primary comparison reports a risk difference of 0.196 and a 95% confidence interval from 0.009 to 0.384. The interval gives a range of values compatible with the observed data under the method used to construct it. In general, confidence intervals express statistical uncertainty; they do not guarantee that the true effect lies inside the interval, nor do they show the probability that a particular effect value is correct.

The interval has a positive lower endpoint, but that endpoint is close to zero relative to the upper end. The range therefore includes both a small positive contrast and a much larger positive contrast. This is a reminder that the estimate is not precise enough to identify a single effect size. The two arm counts, 21 of 49 and 10 of 43, provide the context for that uncertainty.

The risk-ratio interval, 0.980 to 3.467, and odds-ratio interval, 1.0 to 6.124, also span a range of possible contrasts. Different measures use different scales, so the interval endpoints should be interpreted with their corresponding estimate rather than compared as if they were the same quantity. The registry record does not identify the interval-construction method.

These intervals address sampling uncertainty under the assumptions of their analyses. They do not capture every source of uncertainty, such as missing endpoint observations, measurement issues, analytic choices, or selective reporting. The record does not provide enough information to evaluate all of those sources. Precision is therefore best understood as precision of the posted statistical comparison, not as a guarantee about broader clinical meaning.

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 sample-size section is a planning illustration based on the observed primary effect, not the trial’s original design calculation. Its figures are participants per arm, not total events. The stated assumptions are a two-sided significance level of 0.05, equal allocation between arms, and a normal approximation; the target effect is the stated fraction of the observed effect. The original sample-size justification and design assumptions are not reported in the registry record.

The columns for 80% power and 90% power describe planning targets under those assumptions. In general, power is the chance that a planned study will detect a specified effect if that effect is present and the model assumptions hold. The 90% column uses a higher target probability of detecting the stated effect than the 80% column, and therefore requires a larger planned sample for the same effect scenario. These figures are planning illustrations, not observed power.

The rows consider planning for 100%, 75%, and 50% of the observed effect. A smaller effect is harder to distinguish from random variation, so more participants are generally needed to reach the same power target. This relationship is illustrated in the table and curve. The displayed numbers should not be treated as a recommendation for a future study without considering its endpoint, design, analysis plan, and other assumptions.

The registry record does not report whether the original trial was designed around this endpoint, a different effect size, or another outcome. The illustration should therefore remain separate from the completed trial’s historical design. It describes hypothetical sample sizes under stated assumptions; it does not indicate that the completed study had a particular probability of success.

13. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

n is the number of participants in each arm, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.233; treatment proportion p₁ = 0.429; average p̄ = 0.331.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6653 = 1.3039.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6507 = 0.5476.
4. n = (1.3039 + 0.5476)² / (0.1960)² = 89.2, 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
p0 <- 0.232558139534884                          # control proportion
p1 <- 0.428571428571429                          # treatment proportion
n_per_arm <- function(power, frac = 1) {
  q1 <- p0 + (p1 - p0) * frac               # smaller effect = fraction of the observed difference
  pbar <- (p0 + q1) / 2
  z_b <- qnorm(power)
  ceiling(round((z_a * sqrt(2 * pbar * (1 - pbar)) + z_b * sqrt(p0 * (1 - p0) + q1 * (1 - q1)))^2 / (q1 - p0)^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 (unrounded n per arm)
cat("power.prop.test:", round(power.prop.test(p1 = p0, p2 = p1, power = 0.80)$n, 1), "\n")

# Simulation: how often does the z-test reject at the 80%-power sample size?
set.seed(1788631)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 90 (80% power), 119 (90% power)
 75% of observed effect: n per arm = 154 (80% power), 205 (90% power)
 50% of observed effect: n per arm = 330 (80% power), 441 (90% power)
power.prop.test: 89.2 
Simulated power at n = 90 per arm: 0.809 (20000 replicates)

The simulation draws many pairs of event counts at the planned sample size and counts how often the two-proportion z-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

14. Multiplicity, Missing Data and Analysis Populations

The registry record lists one primary outcome and six secondary outcomes. It does not report a multiplicity strategy for the family of outcomes, such as an adjustment to control the chance of false-positive findings or a prespecified order for testing. The primary comparison is reported with an unadjusted p-value, and the respiratory-symptom comparison is also unadjusted. Without a stated strategy, the primary p-value should not be read as accounting for all outcome comparisons.

In general, multiplicity matters because repeated statistical testing increases the opportunity to observe an apparently unusual result by chance. Adjustments and hierarchical approaches are possible, but the record does not establish that any particular approach was used. No such method should be inferred from the presence of a primary endpoint or from the posted p-values.

The endpoint population consists of treated patients with baseline and end-of-infusion blood samples. The registry does not report a participant-flow account for the primary endpoint, the number randomized to each arm, reasons for missing blood samples, or the method used to handle missing endpoint data. It also does not report whether the main analysis followed an intention-to-treat principle. Consequently, it is not possible to determine from this record whether the endpoint analysis included all randomized participants or how missingness may have influenced the result.

The adverse-event populations at risk are reported separately from the primary endpoint denominators. That difference in analysis populations is not necessarily a problem, but the record does not give enough detail to reconcile each population or describe the inclusion rules. It also does not report a prespecified analysis plan, interim analyses, or detailed model specifications. These gaps limit evaluation of whether the reported analyses followed planned procedures and whether all relevant results are available.

These limitations concern documentation and interpretation; they do not establish that an analysis was improper or that missingness biased the result. They mean that readers cannot verify those aspects from the registry record alone. The posted comparisons should be treated as the results documented in the record, with those uncertainties kept in view.

15. Safety Results

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

Deaths

Other (non-serious) adverse events

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

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: pain in extremity (18.2%), back pain (9.1%), pain (6.8%), non-cardiac chest pain (4.5%), respiratory, thoracic and mediastinal disorders - other, specify (4.5%).

The registry reports serious adverse events in the two safety populations at risk: 14 of 52 participants in the regadenoson arm and 16 of 44 in the placebo arm. The reported number of deaths is 0 in each arm. Other adverse events are reported for 44 of 52 participants in the regadenoson arm and 35 of 44 in the placebo arm. These are counts of participants as recorded, not comparisons adjusted for exposure or follow-up time.

The listed serious-event terms include pain in extremity at 18.2%, back pain at 9.1%, pain at 6.8%, non-cardiac chest pain at 4.5%, respiratory, thoracic and mediastinal disorders - Other, specify at 4.5%, and anemia at 3.8%. The registry record does not provide enough context to establish how terms were grouped, whether a participant could contribute to more than one term, or how event relatedness was assessed. The serious-event counts alone do not establish causation or comparative safety. These figures describe the posted safety record and should be interpreted with the population sizes and the trial’s limited duration in mind.

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

The primary result is a comparison of the proportion meeting a defined biological threshold during a 48-hour infusion. The posted data show more participants meeting that threshold in the regadenoson arm than in the placebo arm, with a positive estimated risk difference and an interval that ranges from a small to a substantially larger positive contrast. This is a statistical description of the endpoint, not a conclusion about clinical benefit.

The endpoint does not directly measure whether participants felt better, left hospital sooner, used less opioid medication, or experienced fewer complications. Those topics appear among the secondary outcomes, but most of their numerical results are not reported in the registry record. A change in a laboratory-based outcome should not be assumed to translate into a change in a clinical outcome.

The primary comparison also applies to treated participants with baseline and end-of-infusion blood samples. The record does not report enough detail to determine how those participants relate to all randomized participants or how missing measurements were handled. The statistical interval does not account for every uncertainty in the design, measurement, analysis, or reporting process.

Nor does the comparison establish that the observed difference was caused by the intervention under every relevant assumption. Randomization and masking are important design features, but the registry record does not describe every procedure needed to assess implementation, analysis populations, or follow-up. The result should be read alongside those limits rather than as a stand-alone verdict.

In general, a trial result can inform a focused scientific question while leaving other questions open. Here, the posted primary result concerns the proportion reaching the specified iNKT-cell reduction threshold. It does not establish the size of any broader clinical effect, the durability of a change beyond the infusion period, or the result for outcomes without posted estimates. The record does not report those conclusions.

17. Why This Trial Matters Statistically

This trial is statistically informative because it illustrates the difference between a binary biological endpoint and a broader clinical claim. The primary measure reduces a change in iNKT-cell activation to whether a participant crosses a specified threshold. That choice gives a clear count for comparison, but it also leaves out information about the amount of change within each threshold category.

The posted comparison demonstrates why an effect estimate should be read together with its confidence interval. The point estimate is positive, but the interval spans from a small positive contrast to a much larger one. A single estimate can make results appear more definite than the data justify; the interval makes the uncertainty visible. The risk difference also expresses an absolute contrast, while the risk ratio and odds ratio describe relative contrasts on different scales.

The record also provides a useful example of the boundary between confirmatory and exploratory interpretation. A primary endpoint is identified, but the registry does not report how the multiple secondary outcomes were handled or document a detailed statistical plan. The unadjusted p-value cannot by itself answer whether the finding would remain persuasive within a broader testing strategy. Similarly, the planning illustrations based on the observed effect are not evidence of the completed trial’s power or original design rationale.

Finally, the difference between endpoint and safety populations shows why analysis denominators matter. The primary endpoint applies to treated participants with two blood samples, whereas adverse events use separately reported populations at risk. Without participant-flow details, readers cannot fully reconstruct how each analysis population arose. The trial is therefore a case study in interpreting a result precisely while separating observed summaries from unreported design and analysis details.

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 what this registry record documents. The primary endpoint is restricted to treated participants with baseline and end-of-infusion blood samples, but the record does not provide a participant-flow account or explain why endpoint observations may be unavailable. It does not report the number randomized to each arm or state whether the primary analysis followed an intention-to-treat principle.

The record does not explain the rationale for the 70% threshold, give details of the laboratory assay, or describe how measurements were classified. It also does not report the exact statistical test, model, analysis plan, or handling of missing data. These omissions make it difficult to assess whether the endpoint definition and analysis procedures were specified before results were known.

Although multiple secondary outcomes are listed, numeric results are not posted for most of them, and no multiplicity procedure is reported. The respiratory-symptom comparison is unadjusted. It is therefore not possible to assess the full pattern of secondary findings or to determine how the trial addressed repeated testing.

The sample-size illustrations use the observed primary effect rather than the trial’s original design assumptions. The original sample-size justification is not reported in the registry record, so the illustrations cannot show whether the trial was planned around a different target effect or endpoint. The record also does not report interim analyses or enough follow-up detail to assess effects beyond the stated infusion period. These limitations narrow the interpretation of the posted result; they do not, on their own, indicate the direction or size of any bias.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: A Phase II Trial of Regadenoson in Sickle Cell Anemia — NCT01788631.
• Registry record last updated 2018-02-07; status last verified 2018-01.
• Results first posted 2018-02-07.
• 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 II trial compared a 48-hour regadenoson infusion with placebo in a randomized, triple-masked, parallel-group design. The primary endpoint counted treated participants with baseline and end-of-infusion blood samples whose iNKT-cell activation fell by 70% or more. The posted endpoint counts were 21 of 49 for regadenoson and 10 of 43 for placebo.

The comparison summary reports a risk difference of 0.196, a 95% confidence interval from 0.009 to 0.384, and an unadjusted p-value of 0.047. This is a short-term biological endpoint, and the estimate should be interpreted with its uncertainty and the endpoint-specific population in view. The registry record does not report the original sample-size justification, a detailed statistical analysis plan, or a multiplicity strategy. Numeric results are not reported for most listed secondary outcomes.