A Study of the Safety and Tolerance of Regadenoson in Subjects With Asthma or Chronic Obstructive Pulmonary Disease: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study of the Safety and Tolerance of Regadenoson in Subjects With Asthma or Chronic Obstructive Pulmonary Disease (NCT00862641), a randomized phase 4 study. The primary outcome is Percentage of Subjects Who Had a >15% Decrease in Forced Expiratory Volume in 1 Second (FEV1) at the 2-hour Postbaseline Assessment.

2. Clinical Question

3. Trial Design

This was a Phase 4, randomized, double-blind, parallel-group, placebo-controlled study. The registry record lists enrollment of 1009 and a completed status. The listed study start was 2009-04 and primary completion was 2009-10. Astellas Pharma Inc is listed as the sponsor.

The study included four groups: placebo and regadenoson among subjects with asthma, and placebo and regadenoson among subjects with COPD. Regadenoson was administered as a 0.4mg / 5mL intravenous bolus injection. The placebo was a matching intravenous bolus injection. Randomization and double blinding are stated in the registry record, but the method used to generate the allocation sequence, the allocation concealment procedure, and the details of how blinding was maintained are not reported in the registry record.

The primary endpoint analysis population was the Safety Analysis Set. It included all randomized subjects who received any amount of study drug. The analyzed group sizes were 176 for placebo and 356 for regadenoson in asthma, and 151 for placebo and 316 for regadenoson in COPD. These endpoint analysis sizes are not interchangeable with the overall enrollment count: the registry record defines the analyzed population by treatment receipt and reports separate group counts for the endpoint.

The primary assessment was made 2 Hours post dose. The registry record also lists secondary measures covering short-acting bronchodilator use, changes in spirometric measures and oxygen saturation at the 2-hour post-dose assessment, and selected respiratory adverse events. The protocol’s original sample-size rationale, planned interim analyses, and full statistical 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.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The number of participants analyzed per arm represents Safety Analysis Set (SAF) which included all randomized subjects who received any amount of study drug.

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Subjects Who Had a >15% Decrease in Forced Expiratory Volume in 1 Second (FEV1) at the 2-hour Postbaseline Assessment, measured over 2 Hours post dose.

The primary endpoint was the percentage of subjects who had a >15% decrease in forced expiratory volume in 1 second (FEV1) at the 2-hour postbaseline assessment. FEV1 is the volume of air exhaled during the first second of a forced expiratory maneuver; in this study it was obtained by spirometry. The endpoint turns an individual change in a measured lung-function value into a binary event: each analyzed subject either met the specified decrease threshold or did not.

A threshold-based endpoint can make a clinically interpretable event count possible and allows the event proportion to be compared between randomized groups. It also simplifies the comparison to an occurrence or non-occurrence at the specified assessment rather than describing the full distribution of FEV1 changes. That simplification has a cost: subjects with different magnitudes of change may be grouped together if they both cross the threshold, while changes that do not cross it are not counted as primary events.

The two-hour assessment defines a short-term measurement window. This endpoint does not, by itself, describe changes at other times, the duration of any change, or every aspect of respiratory safety. The registry record’s stated population is the Safety Analysis Set, including randomized subjects who received any amount of study drug.

7. Results Posted in the Registry

• Regadenoson - Asthma: 1.1% (4/356) versus 2.8% (5/176) on control; risk difference -1.7 percentage points (95% CI -4.4 to 1.0), risk ratio 0.40 (0.11–1.45); unadjusted two-proportion z-test p = 0.148.
• Placebo - COPD: 5.3% (8/151) versus 2.8% (5/176) on control; risk difference 2.5 percentage points (95% CI -1.9 to 6.8), risk ratio 1.86 (0.62–5.58); unadjusted two-proportion z-test p = 0.257.
• Regadenoson - COPD: 4.1% (13/316) versus 2.8% (5/176) on control; risk difference 1.3 percentage points (95% CI -2.0 to 4.6), risk ratio 1.45 (0.52–4.00); unadjusted two-proportion z-test p = 0.471.

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.

Use of Short-acting Bronchodilators for Treatment of Symptoms After Study Drug Administration

• 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 - Asthma: 0.3% (1/356) versus 0.6% (1/176) on control; risk difference -0.3 percentage points (95% CI -1.5 to 1.0), risk ratio 0.49 (0.03–7.86); unadjusted two-proportion z-test p = 0.610.
  • Placebo - COPD: 1.3% (2/151) versus 0.6% (1/176) on control; risk difference 0.8 percentage points (95% CI -1.4 to 2.9), risk ratio 2.33 (0.21–25.46); unadjusted two-proportion z-test p = 0.475.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Regadenoson - Asthma 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 Placebo - COPD and the control. The interval gives the range of effects that remain compatible with the data.

The registry record lists secondary outcomes spanning short-acting bronchodilator use, spirometric changes, oxygen saturation, and selected respiratory adverse events. These measures broaden the assessment beyond the primary threshold-based FEV1 outcome: some address rescue medication use, while others describe lung-function or oxygenation measures at the two-hour post-dose assessment. Together, the outcomes indicate that the study considered several related aspects of short-term respiratory response.

For short-acting bronchodilator use within 2 Hours of study drug administration, the posted counts are 1 in each asthma group and 2 in each COPD group. Numerical results for the other listed secondary outcomes are not reported in the registry record. The available secondary information therefore does not support a complete comparison across all listed measures or a detailed account of how each changed between treatment groups.

These secondary measures can help place the primary result in context, but they do not replace the primary endpoint. They assess different outcomes, and some may use different scales or summaries. The primary result concerns the proportion crossing a specified FEV1 decrease threshold at one assessment; a change in another spirometric measure, oxygen saturation, or medication use would answer a related but distinct question.

Unadjusted secondary results carry less weight as confirmatory evidence when several outcomes are examined. In general, testing multiple outcomes increases the chance that some results may appear unusual by chance, unless the analysis plan accounts for multiplicity. The registry record does not report whether a multiplicity adjustment or prespecified hierarchy was used. The secondary outcomes are therefore best treated as descriptive context, particularly where the posted numerical information is incomplete, rather than as an independent basis for a firm conclusion.

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

• Use of Short-acting Bronchodilators for Treatment of Symptoms After Study Drug Administration
• Use of Short-acting Bronchodilators for Treatment of Symptoms After Study Drug Administration
• Change From Baseline to the 2 Hour Post-dose Assessment for FEV1 Absolute Values
• Change From Baseline to the 2 Hour Post-dose Assessment for FEV1 Percent Predicted
• Change From Baseline to the 2 Hour Post-dose Assessment for Forced Vital Capacity (FVC)
• Change From Baseline to the 2 Hour Post-dose Assessment for FEV1/ FVC Ratio
• Change From Baseline to the 2 Hour Post-dose Assessment for Oxygen Saturation Measured by Pulse Oximetry
• Percentage of Selected Respiratory Adverse Events

9. Statistical Interpretation

10. Statistical Methods Explained

What does randomization contribute?

Randomization assigns participants to study groups by chance, with the aim of making the groups comparable on average before treatment. In this study, assignment was randomized and the comparison was double-blind. Those design features can reduce the influence of some systematic differences and expectations on the comparison, but they do not guarantee that every group characteristic is identical. The registry record does not report the randomization sequence method or allocation concealment details, so those implementation features cannot be assessed from the record.

The parallel-group design means that participants were assigned to a study group and the groups were compared over the assessment period. The placebo injection was described as matching the regadenoson injection. Separate asthma and COPD groups mean that the relevant treatment comparisons should be made within each condition. Comparing a COPD group directly with an asthma group would mix treatment assignment with differences between the conditions.

How should a binary endpoint be analyzed?

The primary outcome is binary because each subject either had a >15% decrease in FEV1 at the two-hour assessment or did not. For a binary outcome, a basic summary is the proportion of participants with the event in each group. A risk difference describes the difference between two event proportions; a value below zero means the first group’s observed proportion is lower than the reference group’s, and a value above zero means it is higher. The effect measure is tied to the group order, so the comparison groups must be identified before interpreting its direction.

In the posted results, the sponsor reported Cochran-Mantel-Haenszel analyses for placebo versus regadenoson within asthma and within COPD. This method is a stratified approach to comparing binary outcomes. The registry record reports p-values for these analyses but does not report a treatment-effect estimate or confidence interval alongside them. A p-value addresses how compatible the observed data are with a specified null hypothesis under the analysis assumptions; it does not give the size of an effect, the probability that the null hypothesis is true, or the probability that a result will be replicated.

The recalculated values are unadjusted calculations from posted summary statistics. They are useful as a simple check and a way to describe the observed comparison, but they are not a replacement for the sponsor’s stated analysis. In particular, a recalculation against a shared asthma-placebo reference does not constitute the within-COPD randomized treatment comparison. The condition-specific sponsor analyses preserve the intended treatment contrast within each study population.

What do confidence intervals add?

A confidence interval describes a range of effect values compatible with the data under a specified method. It conveys both the direction and the precision of an estimate. If an interval for a risk difference includes zero, the data are compatible with no difference as well as with differences in either direction at the interval’s confidence level. That does not prove there is no difference. When event counts are sparse, intervals can be broad because the data provide limited information about the underlying event proportions.

The sponsor’s posted analysis reports 95% confidence-interval confidence levels but does not give interval bounds or effect estimates. The recalculated comparisons include intervals based on summary statistics, but the shared reference groups mean those comparisons need careful interpretation. Any numerical interval should be understood in relation to the exact contrast it represents, not treated as a general interval for all treatment comparisons in the trial.

Why distinguish the analysis population?

The primary endpoint analysis used the Safety Analysis Set: randomized subjects who received any amount of study drug. The registry record does not report a separate intention-to-treat analysis population for this endpoint. An analysis limited to participants who received study drug can differ from an analysis of everyone randomized if some randomized participants did not receive treatment or lack an outcome assessment. The record does not provide enough information to determine whether that occurred or how any missing endpoint data were handled.

General statistical principle: missing outcomes can affect an estimate if the probability of missingness is related to treatment assignment or the outcome. The direction and magnitude of such effects depend on why data are missing and on the analysis approach. The registry record does not report missing-data methods, so no conclusion about their influence is possible.

What can the p-values say?

A p-value summarizes how unusual data at least as inconsistent with a null model would be if that null model and the analysis assumptions were true. It is not a measure of clinical importance or precision. A p-value above a conventional threshold does not establish equivalence, and a p-value below a threshold would not, by itself, establish that an observed difference is important. The registry record does not report an equivalence or non-inferiority margin for this outcome.

The sponsor used the Cochran-Mantel-Haenszel method for the reported condition-specific analyses. The recalculations use unadjusted summary-statistic comparisons and can therefore differ from the sponsor’s p-values without implying that one calculation is erroneous. No discrepancy was flagged between the sponsor analysis and recalculation. The sponsor’s stated analysis remains the primary registry analysis, while recalculated quantities are supplementary descriptions rather than a new confirmatory analysis.

11. Confidence Intervals and Precision

The observed event percentages are based on relatively few events: 5 in the asthma placebo group, 4 in the asthma regadenoson group, 8 in the COPD placebo group, and 13 in the COPD regadenoson group. Those counts matter because a percentage can appear stable while being based on only a small number of participants who met the endpoint. The group sizes were also unequal within each condition, with 176 and 356 analyzed in asthma and 151 and 316 in COPD.

The recalculated confidence intervals for the displayed comparisons include values on both sides of zero. This means the summary data are compatible with a negative as well as a positive risk difference for those particular comparisons. The widths of the intervals indicate that the estimates are not precise enough to pin down a narrow range of plausible differences. The comparison involving COPD groups against the asthma placebo reference should not be mistaken for a direct within-COPD treatment estimate.

The sponsor reported 95% confidence-interval confidence levels for its Cochran-Mantel-Haenszel analyses, but interval bounds and effect estimates are not reported in the registry record. Consequently, the precision of the sponsor’s own treatment estimates cannot be judged from the posted analysis alone. A p-value without an effect estimate and interval gives less information about the range of plausible treatment differences.

In general, confidence intervals are not guarantees that the true value lies within a particular interval. They are a way to express uncertainty under the chosen model and procedure. Here, the small event counts and missing sponsor interval bounds limit how sharply the treatment contrasts can be described. The data are compatible with no clear separation in the primary outcome, but they do not establish exact similarity between groups.

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 illustrations express the number of participants needed per arm for the binary outcomes in this analysis. They are not total event counts. Each row considers planning for a stated fraction of the observed effect: 100% of the observed effect, 75% of the observed effect, or 50% of the observed effect. For each assumed effect, the 80% power column gives the illustrated number of participants per arm for a design with an 80% chance of detecting that effect under the stated assumptions; the 90% power column gives the corresponding number for a 90% chance.

The illustrations use a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. They are computed from the observed effect and are not the original design assumptions for this trial. The original sample-size justification and design assumptions are not reported in the registry record. Smaller effects are harder to distinguish from random variation and therefore require more participants under the same planning approach. The rows are planning scenarios, not observed trial results.

These values are not observed power. They do not tell how much power the completed study actually had after observing its results. Rather, they show how the indicated assumptions translate into approximate per-arm sample sizes for future planning. Because observed effects can be unstable, particularly when the event counts are small, planning directly from an observed effect should be interpreted cautiously. The sample-size figures are illustrations, not recommendations or evidence that the trial was designed around those exact values.

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 = 0.028; treatment proportion p₁ = 0.011; average p̄ = 0.020.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.1971 = 0.3864.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.1968 = 0.1656.
4. n = (0.3864 + 0.1656)² / (-0.0172)² = 1,033.0, rounded up to 1,034 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 <- 0.0284090909090909                          # control proportion
p1 <- 0.0112359550561798                          # 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(862641)
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 = 1,034 (80% power), 1,383 (90% power)
 75% of observed effect: n per arm = 2,033 (80% power), 2,720 (90% power)
 50% of observed effect: n per arm = 5,010 (80% power), 6,706 (90% power)
power.prop.test: 1033 
Simulated power at n = 1,034 per arm: 0.822 (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. Analyses Reported by the Sponsor

The sponsor reported separate Cochran-Mantel-Haenszel analyses for the asthma groups and the COPD groups. The reported p-values were above 0.05 in both comparisons. The registry record does not provide the sponsor’s effect estimates or the bounds of the reported 95% confidence intervals, which limits direct assessment of the size and precision of those analyses.

The recalculated results use unadjusted calculations from posted summary statistics. The asthma recalculation compares the regadenoson asthma group with placebo asthma. For COPD, the displayed recalculations use placebo asthma as the shared reference, not placebo COPD; those values should not be read as direct randomized treatment effects within COPD. The primary treatment comparison in COPD is regadenoson versus placebo among subjects with COPD, as analyzed in the sponsor’s condition-specific analysis.

The sponsor analysis and the recalculations use different approaches, so their p-values need not be identical. No discrepancy was flagged between the sponsor analysis and the recalculation. The sponsor’s own condition-specific analysis is the central registry result; the simple unadjusted calculations provide supplementary context and should not override it. Neither analysis, on the reported information, establishes equivalence or proves that the treatment groups have identical event rates.

15. Multiplicity, Missing Data and Analysis Populations

The registry record lists multiple secondary outcomes in addition to the primary endpoint. It does not report whether the statistical analysis plan specified a hierarchy among outcomes, adjusted significance thresholds for multiple testing, or a procedure to control the overall chance of false-positive findings. Without those details, isolated secondary p-values, if available, would need cautious interpretation. The record does not post numerical results for most of the listed secondary measures, and no full account of analyses across outcomes is available.

In general, multiplicity matters because examining many hypotheses creates more opportunities for a result to appear notable by chance. Adjustment methods or a prespecified testing sequence can address this issue, but no such method is reported in the registry record. This absence does not establish that no adjustment was made; it means the method is not reported in the registry record.

The primary analysis population is described as the Safety Analysis Set, including randomized subjects who received any amount of study drug. The record does not report how many randomized subjects did not receive study drug, whether all analyzed subjects had an FEV1 assessment, or how missing assessments were handled. It also does not state whether any participants were excluded after randomization or give reasons for missing outcome data. These omissions limit assessment of possible selection or missing-data effects.

The registry record does not report the original sample-size justification, the target effect used in planning, planned interim analyses, or a complete statistical analysis plan. It also does not provide sponsor effect estimates and interval bounds for the primary analyses. These missing details restrict independent evaluation of the planned analysis, precision, and handling of multiple outcomes. Conclusions should remain tied to the results that are actually reported rather than filling these gaps with assumptions about the protocol.

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: bradycardia (0.3%), electrocardiogram change (0.3%), nephrolithiasis (0.3%), amyotrophic lateral sclerosis (0.3%), atrioventricular block complete (0.3%).

Serious adverse events were reported for 0 subjects in the placebo asthma group, 2 in the regadenoson asthma group, 0 in the placebo COPD group, and 4 in the regadenoson COPD group. The groups at risk were 176, 356, 151, and 316, respectively. These are group-level counts from the registry record; they do not establish whether an event was caused by study treatment.

The registry record lists six top serious adverse event terms, each at 0.3%: bradycardia, electrocardiogram change, nephrolithiasis, amyotrophic lateral sclerosis, atrioventricular block complete, and rectal hemorrhage. The record does not provide further event-level detail in the listed summary. The deaths field is not populated, so death information is not reported in the registry record.

Serious adverse event counts should be interpreted separately from the primary FEV1 endpoint. They describe a different safety category and do not summarize all adverse events or their severity, timing, or relationship to treatment. The registry record also lists other adverse-event counts, but a complete causal assessment cannot be made from aggregate counts alone.

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

The posted primary results describe the percentage of analyzed subjects who crossed a defined FEV1 decrease threshold at the 2-hour postbaseline assessment. The observed percentages were 2.9% with placebo and 1.1% with regadenoson among subjects with asthma, and 5.4% with placebo and 4.2% with regadenoson among subjects with COPD. The event counts were small, and the sponsor’s reported condition-specific p-values were above 0.05.

These findings do not demonstrate that regadenoson and placebo are equivalent. Equivalence requires a prespecified margin and an analysis designed to assess whether the difference lies within that margin; such a margin is not reported in the registry record. Likewise, the results do not prove that there is no treatment-related difference. The available evidence is compatible with uncertainty about the size and direction of any underlying difference.

The primary outcome represents one spirometric threshold at one short-term assessment. It does not establish what happens at other times, how subjects felt, whether other respiratory outcomes changed, or what the longer-term course might be. It also does not summarize all adverse events. Secondary measures cover related questions, but numerical results for most of those outcomes are not reported in the registry record.

The trial enrolled subjects with asthma or COPD under the listed study conditions. Results should not be assumed to apply to populations or clinical settings not described in the registry record. The group percentages are descriptive of the analyzed participants and should be considered together with the small event counts, uncertainty, and limitations in the posted analysis details. They are not, on their own, a basis for medical advice or a complete judgment about safety.

18. Why This Trial Matters Statistically

This trial illustrates how a binary safety endpoint can produce low event counts even when the analyzed groups include hundreds of participants. The primary outcome reduces spirometric change to whether a participant crossed a specified threshold. That makes the result straightforward to count, but it also means the event proportions do not describe the full range of FEV1 changes.

The study’s separate asthma and COPD groups highlight the importance of matching the analysis contrast to the randomized design. A regadenoson-versus-placebo comparison within each condition addresses the treatment contrast in that population. Comparing across conditions instead combines treatment assignment with differences between populations. The sponsor reported condition-specific analyses, while unadjusted recalculations using a shared reference require particular care.

The record also illustrates the difference between a p-value and a treatment-effect estimate. The sponsor’s reported p-values provide a test result, but the absence of reported effect estimates and confidence-interval bounds makes it harder to assess the magnitude and precision of the sponsor’s comparisons. Small event counts further constrain what can be learned from the data.

Finally, the study’s primary endpoint is only one part of the evidence. The listed secondary measures address other respiratory outcomes, but most numerical secondary results are not reported in the registry record. When several outcomes are considered, multiplicity and prespecification matter; the registry record does not report how those issues were handled. These features make the study a useful example of why design, contrast definition, uncertainty, and completeness of reporting all matter when interpreting clinical trial results.

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.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

The primary endpoint is limited to a >15% decrease in FEV1 at the two-hour postbaseline assessment. It does not describe the magnitude of change for every participant, changes outside that assessment, or longer-term outcomes. The binary threshold can obscure differences among participants who do not cross it and among those who do.

Event counts were small in each group, and the group sizes differed between treatment arms and between asthma and COPD. Sparse events limit precision and make percentages sensitive to a small number of observations. The sponsor’s primary-analysis effect estimates and confidence-interval bounds are not reported in the registry record, limiting interpretation of the size of the randomized comparisons.

The available recalculations are unadjusted and use a shared placebo-asthma reference for the COPD group comparisons. Those values are not direct treatment contrasts within COPD. The sponsor’s condition-specific analyses are the appropriate posted comparisons, but their numerical effect estimates are absent. The record does not report an interaction analysis that would assess whether the treatment contrast differs between asthma and COPD.

Further limitations include unreported details about the randomization and allocation procedures, missing-data handling, multiplicity control, original sample-size rationale, and interim analyses. Numerical results for most secondary endpoints are not reported in the registry record. Death information is also not populated. These gaps restrict assessment of the full analysis and safety profile, and they should not be filled by assumptions about methods or findings.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Study of the Safety and Tolerance of Regadenoson in Subjects With Asthma or Chronic Obstructive Pulmonary Disease — NCT00862641.
• Registry record last updated 2012-09-18; status last verified 2012-09.
• Results first posted 2010-12-15.
• 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

NCT00862641 is a completed Phase 4, randomized, double-blind, parallel-group, placebo-controlled study sponsored by Astellas Pharma Inc. It enrolled 1009 subjects with asthma or COPD and compared a 0.4mg / 5mL intravenous bolus injection of regadenoson with matching placebo.

The primary outcome was the percentage with a >15% decrease in FEV1 at the 2-hour postbaseline assessment. In asthma, the posted percentages were 2.9% with placebo and 1.1% with regadenoson; in COPD, they were 5.4% and 4.2%, respectively. The event counts were small, and the sponsor’s reported condition-specific p-values were above 0.05. The registry record does not report sponsor effect estimates or confidence-interval bounds, and numerical results for most secondary outcomes are not reported.