Efficacy and Safety of Nebivolol (Added to Lisinopril or Losartan) in Hypertensive Patients: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Efficacy and Safety of Nebivolol (Added to Lisinopril or Losartan) in Hypertensive Patients (NCT00734630), a randomized phase 4 study. The primary outcome is Mean Seated Trough Cuff Systolic Blood Pressure (SBP) at Week 12.

2. Clinical Question

3. Trial Design

This was a Phase 4, randomized, double-blind, placebo-controlled, parallel-group trial. Its title describes nebivolol added to antihypertensive treatment with lisinopril or losartan in patients with hypertension. Participants were assigned to nebivolol or matching placebo, with both treatments given orally. The registry lists an enrollment of 491. The posted primary-outcome groups include 256 participants in the nebivolol group and 232 in the placebo group; the registry does not explain the difference between the enrollment figure and the outcome-group counts.

The nebivolol arm description lists 5 mg, 10 mg, 20 mg, and 40 mg tablets. The placebo arm used matching tablets. The record does not report the dose-escalation schedule, criteria for choosing or changing a dose, or whether every participant could receive each listed dose. Those details should not be inferred from the list of available doses.

The primary completion date is 2010-03, and the study status is completed. The study start is recorded as 2008-08. The primary endpoint was mean seated trough cuff systolic blood pressure at Week 12, described as change from baseline at Visit 5 (Week 0) to Visit 10 (Week 12), using last observation carried forward. A secondary outcome was mean seated trough cuff diastolic blood pressure at Week 12 over the same timeframe.

Although the record identifies randomization and double masking, it does not describe the sequence-generation procedure, allocation concealment, masking checks, or the statistical analysis plan. The original sample-size justification, planned analysis populations, and any interim analyses are not reported in the registry record. The available posted results therefore support a description of the design and reported endpoint summaries, but not a reconstruction of every operational or analytic feature.

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: Placebo washout phase was required for patients currently on anti-hypertensives at screening followed by a losartan or lisinopril run-in phase before assignment to Placebo or Nebivolol arms. Patients who were untreated at screening started the study at the open-label lead-in phase.

Overall Study

Reasons for not completing this period:

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 Mean Seated Trough Cuff Systolic Blood Pressure (SBP) at Week 12, measured over From baseline Visit 5 (Week 0) to Visit 10 (Week 12).

The primary endpoint is the change from baseline in mean seated trough cuff systolic blood pressure at Week 12. It is a continuous measurement, expressed in mmHG, and the registry describes it as a mean with standard deviation. “Change from baseline” compares the measurement at the designated follow-up with the baseline measurement. A negative mean change in this context indicates a lower average follow-up value than baseline; it does not by itself establish a difference between treatment groups.

Seated trough cuff measurement refers to blood pressure measured while seated at the designated trough assessment. A standardized measurement and a specified assessment time can make group summaries more interpretable, because they define what was measured and when. The registry record does not provide further detail about measurement procedures, the timing of medication relative to measurement, or the number of readings used.

The endpoint is used to compare average changes between the randomized groups, rather than to describe only what happened within either group. Both posted arm means are reductions, so the central comparison is the difference between those average changes. The endpoint description specifies last observation carried forward (LOCF), a method for substituting an earlier observed value when a later value is missing. That choice affects which values contribute to the Week 12 summary and is relevant when interpreting the result. The reasons for missing measurements and the amount of missingness are not reported in the registry record.

7. Results Posted in the Registry

• Nebivolol: mean -10.10 versus -7.30 on control; difference -2.80 (95% CI -5.71 to 0.11), standardized effect d = -0.17; z-test p = 0.059.

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.

Mean Seated Trough Cuff Diastolic Blood Pressure (DBP) at Week 12

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Nebivolol: mean -7.80 versus -3.50 on control; difference -4.30 (95% CI -6.14 to -2.46), standardized effect d = -0.42; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Nebivolol than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The posted secondary outcome is mean seated trough cuff diastolic blood pressure change at Week 12. Its arm summaries and unadjusted comparison point in the same general direction as the primary systolic outcome, while the secondary comparison is more clearly separated from zero in its unadjusted calculation. This directional consistency can be viewed as supportive context: the two blood-pressure measures do not present opposing patterns in the posted summaries.

That consistency does not make the secondary result a confirmation of the primary result. The outcomes measure different components of blood pressure and are statistically related, so agreement in direction is informative but not equivalent to an independent replication. The registry does not report a prespecified testing hierarchy or a multiplicity adjustment. Without that information, the nominal evidence from an unadjusted secondary comparison should be interpreted cautiously, especially when considering the possibility of multiple outcome tests or analyses.

Multiplicity matters because the chance of obtaining at least one apparently persuasive result can increase when several hypotheses are tested. Adjustments or a clearly specified hierarchy can help control that risk, but no such approach is reported in the registry record. The record also lists no reported analyses, so it does not establish whether the posted secondary comparison was planned in the same way as the primary comparison or whether other outcomes were examined.

The most balanced reading is to treat the secondary pattern as supportive but exploratory. It can help describe the broader endpoint pattern, but it cannot resolve the primary interval’s uncertainty, establish clinical importance, or compensate for missing information about the analysis plan and missing-data handling. Its evidentiary weight is lower than a primary result interpreted under a clearly reported, prespecified testing strategy.

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

• Mean Seated Trough Cuff Diastolic Blood Pressure (DBP) at Week 12

9. Statistical Interpretation

10. Statistical Methods Explained

The registry presents continuous outcomes as group means with standard deviations. A mean describes the average change in the group, while the standard deviation describes how dispersed individual measurements are around that average. The mean is useful for describing the central group-level change, but it does not show whether every participant changed in the same direction or by a similar amount. The standard deviation is not the uncertainty interval for the treatment contrast; it describes variation among participant measurements.

What does the between-group estimate represent?

The reported mean difference compares the nebivolol group’s mean change with the placebo group’s mean change. The posted arm means are -10.1 and -7.3 mmHG, respectively, and the unadjusted recalculation gives a difference of -2.8 mmHG. Because the endpoint is a change from baseline, a more negative group mean represents a greater average reduction. The comparison is the relevant contrast for the randomized groups; it is not enough to observe that each group changed from baseline, since changes can occur in both arms for many reasons.

A treatment contrast is an estimate, not a guarantee that the true effect equals its point value. Sampling variability means that results from another comparable sample could differ. The confidence interval expresses a range of values reasonably compatible with the observed data under the calculation’s assumptions. If that interval includes zero, the data do not distinguish the estimated contrast from no difference at the stated confidence level. This does not prove that the groups are identical; it indicates that the estimate is uncertain enough to include that possibility.

What does the recalculated p-value tell the reader?

The primary comparison’s unadjusted recalculated p-value is 0.059. A p-value measures how unusual data at least as incompatible with a specified no-difference model would be, assuming that model and the calculation assumptions hold. It is not the chance that the no-difference model is true, and it does not quantify the probability that the result arose “by chance” in an everyday sense. It also does not measure clinical importance. Its interpretation belongs alongside the effect estimate, interval, design, and analysis limitations.

The posted comparison is labeled as an unadjusted recalculation from summary statistics. It is not a reconstruction of a model with covariates, stratification, repeated measures, or other adjustments. The registry record does not report the sponsor’s analysis methods or a formal analysis result. Consequently, the recalculated p-value and interval should be understood as descriptive inferential summaries from the posted data, not as a substitute for a prespecified trial analysis.

Why do the standard deviations matter?

Standard deviations describe the participant-to-participant spread around each arm’s mean. When spread is large relative to the observed difference between group means, the group contrast is estimated less precisely for a given sample size. The primary endpoint has substantial variation within each group compared with the mean difference. This helps explain why the interval around the contrast is not narrow enough to exclude zero. It does not identify why participants varied, and it does not imply that the mean is uninformative.

In general, over-dispersion means that observed variation is larger than a model assumes. If an analysis assumes less variability than is present, its uncertainty estimates may be too small and its conclusions too confident. Conversely, a larger genuine spread generally makes a group difference harder to estimate precisely. These are general statistical principles; the registry does not report an over-dispersion assessment or a model-based variance analysis for this trial.

How does LOCF affect the endpoint?

The primary endpoint is described as using last observation carried forward. LOCF fills a missing follow-up measurement with the participant’s most recent earlier measurement. It can retain participants with incomplete follow-up in a summary, but it imposes an assumption: that carrying the earlier value forward is an appropriate representation of the missing Week 12 value. That assumption may not hold if blood pressure would have changed after the last observed measurement.

LOCF can also make uncertainty appear different from what would result under other missing-data methods, depending on why measurements are missing and how participant values evolve. The registry record does not report the extent or pattern of missing data, the reasons for missingness, or sensitivity analyses using alternative assumptions. It is therefore not possible to assess from the record whether LOCF materially affected the reported means or the comparison.

What can be inferred from the secondary outcome?

The secondary endpoint is another continuous change measure, mean seated trough cuff diastolic blood pressure at Week 12. Its posted unadjusted comparison is in the same general direction as the primary comparison. The record does not report a formal hierarchy of endpoints, multiplicity adjustment, or a sponsor analysis of the secondary outcome. When more than one outcome is examined, an apparently strong unadjusted result may arise more readily by chance across the set of tests. The secondary result therefore adds context but carries less confirmatory weight than a prespecified primary analysis with a documented multiplicity strategy.

The registry lists one posted secondary outcome and no reported analyses. A count of posted outcomes is not a complete account of every comparison that may have been considered during the study. The analysis plan and any additional exploratory tests are not reported in the registry record, so the full scope of multiplicity cannot be established.

11. Confidence Intervals and Precision

The primary mean-difference estimate is -2.8 mmHG, with a 95% confidence interval from -5.711 to approximately 0.111 mmHG. The interval is centered around the estimated contrast and communicates the uncertainty associated with that estimate under the recalculation. Its width matters: the data remain compatible with a more substantial reduction in the nebivolol group, but also with little or no difference and a small contrast in the opposite direction. The interval crossing zero is consistent with the unadjusted p-value of 0.059.

A confidence interval is not a range containing a fixed proportion of individual participants’ blood-pressure changes. Nor does it mean that there is a 95% probability that the true effect lies within this particular interval. In general, the stated confidence level describes the long-run coverage property of the method when its assumptions hold across repeated samples. For this trial, the interval is an unadjusted recalculation from the posted summary statistics, not an interval reported as a sponsor analysis.

The interval gives more information than a threshold judgment based only on a p-value. It shows the range of effect sizes that remain reasonably compatible with the data, while the point estimate alone can suggest more certainty than is warranted. The upper limit is slightly above zero, so the interval does not rule out no between-group difference. The record does not provide a prespecified threshold for a clinically important difference, so the clinical importance of values within the interval cannot be judged from the registry outcome data alone.

Precision is influenced by the number of observations and the variability in measurements. The posted outcome groups contain 256 and 232 participants, and the standard deviations are 16.9 and 15.9 mmHG. Those quantities help describe the basis for the uncertainty calculation, but they do not remove uncertainty or account for unreported features of the trial analysis. Missing-data handling, analysis population, and any adjustments could also influence an inferential result, and those details are not fully reported in the registry record.

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 display gives planning illustrations in participants per arm, not total event counts. The calculations use the observed effect as a reference and show planning for 100%, 75%, and 50% of that observed effect. They assume a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The original trial’s design assumptions and sample-size justification are not reported in the registry record. These figures are planning illustrations, not observed power.

The 80% power column gives the approximate number of participants per arm in a hypothetical study that would have an 80% probability of detecting the specified effect under the listed assumptions, if that effect and the assumptions were correct. The 90% power column gives the corresponding planning count for a higher target probability of detecting that effect. Power is a design property under stated assumptions; it is not a measure of how likely the observed result is true, and the planning values do not retroactively describe the power of this completed trial.

For the primary endpoint, planning for the full observed effect corresponds to 541 participants per arm for 80% power and 724 participants per arm for 90% power. Planning for 75% of the observed effect corresponds to 962 and 1,287 participants per arm, respectively. Planning for 50% corresponds to 2,163 and 2,896 participants per arm, respectively. These counts increase as the effect to be detected becomes smaller, because a smaller contrast is harder to distinguish from random variation.

The same principle applies to the secondary outcome’s planning figures, but the outcome-specific values should not be treated as evidence that the trial was designed around that endpoint. The calculations use the observed effect, which can be an unstable basis for future planning, particularly when the observed estimate is uncertain. Planning decisions normally require assumptions chosen before results are known, together with the study’s goals and analytic plan; those original choices are not reported in the registry record.

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, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = -2.800; pooled standard deviation σ = 16.432.
2. n = 2 × (1.96 + 0.842)² × 16.432² / -2.800² = 540.7, rounded up to 541 participants per arm for 80% power.

The smaller-effect rows in the table above repeat the same calculation with the effect multiplied by 0.75 and 0.5 (for ratios, applied to the logarithm of the ratio).

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
delta <- -2.8                      # observed difference in means
sigma <- 16.432281537973                     # pooled standard deviation
n_per_arm <- function(power, frac = 1) {
  ceiling(round(2 * (z_a + qnorm(power))^2 * sigma^2 / (delta * frac)^2, 6))
}
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: n per arm = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(n_per_arm(0.80, f), big.mark = ","), format(n_per_arm(0.90, f), big.mark = ",")))

# Check against R's built-in function (t-based, so very slightly larger)
cat("power.t.test:", round(power.t.test(delta = delta, sd = sigma, power = 0.80)$n, 1), "\n")

# Simulation: exact two-sample t-test using simulated means and variances
set.seed(734630)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 541 (80% power), 724 (90% power)
 75% of observed effect: n per arm = 962 (80% power), 1,287 (90% power)
 50% of observed effect: n per arm = 2,163 (80% power), 2,896 (90% power)
power.t.test: 541.6 
Simulated power at n = 541 per arm: 0.804 (20000 replicates)

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

14. Multiplicity, Missing Data and Analysis Populations

The registry identifies one primary outcome and one secondary outcome, but does not report a statistical analysis plan, a testing hierarchy, or a method for controlling multiplicity. Multiplicity arises when investigators make several statistical comparisons: even if each test is judged separately, the chance of at least one nominally unusual result can rise across a collection of tests. A prespecified hierarchy or adjustment can address this issue, but neither is documented in the registry record. The unadjusted secondary result should therefore not be treated as if it had the same confirmatory status as a primary result protected by a reported plan.

The registry lists no reported analyses for either posted outcome. The available mean differences, confidence intervals, and p-values are unadjusted recalculations from posted group summaries. The record does not state whether the trial sponsor conducted an adjusted analysis, which model might have been used, or whether that analysis was prespecified. As a result, these recalculations should be distinguished from a complete report of the trial’s inferential analysis.

The primary outcome description specifies LOCF, but the record does not give the number of participants with missing measurements, reasons for missingness, timing of missing values, or results from sensitivity analyses. LOCF assumes an earlier observed value is an adequate stand-in for a later missing value. If missingness is related to participant characteristics or changes over time, that assumption may affect the estimated group means. The available record does not permit an evaluation of the direction or magnitude of any such influence.

The endpoint description does not identify the analysis population, such as whether all randomized participants were included, or how protocol deviations and incomplete follow-up were handled. Details of randomization and allocation concealment are also not reported. These omissions limit assessment of the analysis population and potential departures from the assigned treatment comparison. They do not demonstrate that a particular bias occurred; they mean that the registry record does not supply enough information to evaluate these questions fully.

15. Safety Results

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

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

Most frequent serious adverse event terms

Serious events with the highest arm-level rate: angioedema (0.4%), non-cardiac chest pain (0.4%), acute pancreatitis (0.4%), anxiety (0.4%), cellulitis (0.4%).

The registry reports serious adverse events for 258 participants at risk in the nebivolol group, with 1 affected, and 233 at risk in the placebo group, with 3 affected. These are counts, not a full description of event timing, duration, severity beyond the serious classification, or relationship to treatment. The record does not report deaths for either group, so mortality counts cannot be interpreted from these entries.

The record lists five serious adverse-event terms, each shown at 0.4%: angioedema, non-cardiac chest pain, acute pancreatitis, anxiety, and cellulitis. The listed terms are not linked to a treatment group in the posted summary, so they should not be assigned to either arm. Counts for the other adverse-event category are recorded as zero affected in both groups; this does not establish that no non-serious events of any kind occurred.

Serious adverse-event summaries are descriptive and depend on the definitions, follow-up, reporting, and attribution procedures used in the trial. The registry record does not provide enough detail to compare safety comprehensively or to infer that an event was caused by a study treatment. The figures should be read as the adverse-event counts recorded in the registry, not as a complete assessment of risks.

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

The posted results describe average blood-pressure changes over the specified follow-up and compare those changes between the randomized groups. On the primary endpoint, the estimated contrast is in the direction of a larger average reduction in the nebivolol group, but the unadjusted interval includes zero. Thus, the estimate has meaningful uncertainty: the registry summary does not establish a precise nonzero difference, but it also does not show that the groups are equivalent.

The result does not establish whether any observed difference is clinically important. The registry record does not report a threshold for a meaningful change, nor does it provide patient-level outcomes that would connect the average measurement change to symptoms, complications, or other clinical outcomes. Statistical evidence about an average blood-pressure measure should not be extended to claims about outcomes that were not reported.

The trial’s randomized, double-blind, placebo-controlled design is relevant to interpreting a group comparison, but the registry record does not describe important operational details or a full analysis plan. The primary endpoint uses LOCF, while missing-data quantities and sensitivity analyses are not reported. The outcome analysis population is also unspecified. These gaps restrict how confidently the posted summaries can be generalized to the complete trial analysis.

The secondary endpoint has a direction consistent with the primary outcome, but its unadjusted status and the absence of a documented multiplicity plan limit the strength of that supporting evidence. The registry lists no reported analyses, and the displayed recalculations do not replace a sponsor analysis if one exists outside the record. Together, these points mean that the posted results are best interpreted as a statistical description of the registered summaries, with uncertainty and reporting limitations made explicit.

Nothing in these results alone establishes an individual response, a lasting effect beyond the measured follow-up, or an effect in populations not described by the trial. The record does not report long-term outcomes or subgroup results. These are limits on what can be concluded from the registry data, not evidence for or against an unreported outcome.

17. Why This Trial Matters Statistically

This trial is statistically useful because it illustrates the distinction between within-group change and a randomized between-group comparison. Both arms have negative mean changes in the primary endpoint, but the comparison asks whether their average changes differ. Looking only at the decline in one group would not answer that question. The randomized placebo comparison is the relevant framework for separating the observed arm contrast from changes that may occur in both arms.

It also illustrates why the estimate, confidence interval, and p-value should be read together. The point estimate has a direction and magnitude, but the interval includes zero and the unadjusted p-value is 0.059. A threshold-only account would obscure the range of effects compatible with the data. Reporting the interval makes the uncertainty around the treatment contrast more visible and discourages a simple yes-or-no reading.

The posted result also shows how endpoint handling and reporting completeness shape interpretation. LOCF is specified for the primary outcome, but missingness and sensitivity analyses are not described. The analysis population and sponsor analysis are not reported. Those omissions matter because a statistical result is not only a number: it depends on which participants and measurements enter the calculation and on the assumptions used for incomplete data.

Finally, the secondary endpoint and planning illustrations show two additional statistical principles. Secondary findings require care when multiplicity plans are absent, and planning counts depend strongly on the effect size chosen for detection. The displayed planning counts are illustrations based on observed effects, not evidence of the trial’s original design adequacy. Overall, this record is a practical example of how a clear numerical estimate can coexist with substantial uncertainty and incomplete information about the analysis.

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.

A key trial-specific limitation is that the primary endpoint is reported using LOCF, while the registry does not report how many measurements were missing, why they were missing, or whether alternative missing-data analyses were performed. The appropriateness of carrying an earlier value forward depends on how measurements change after the last observed visit. Without the missingness pattern or sensitivity results, the stability of the primary estimate under other assumptions cannot be assessed.

The registry does not identify the endpoint analysis population. Although enrollment and outcome-group counts are recorded, the record does not explain how participants with incomplete follow-up, protocol deviations, or other analysis exclusions were handled. It also does not provide the trial’s original sample-size justification or statistical analysis plan. These omissions prevent a direct comparison between the posted summary-statistic recalculation and any prespecified sponsor analysis.

The primary confidence interval is compatible with no difference, and the record does not define a clinically meaningful threshold for the endpoint. Consequently, neither statistical precision nor clinical importance can be fully characterized from the registry results alone. The secondary outcome has an unadjusted comparison, but no multiplicity approach is described; this limits how much confirmatory weight that result can carry.

The registry title and summary identify patients with hypertension taking lisinopril or losartan, but detailed eligibility criteria and subgroup results are not reported. Dose options are listed, but dose-selection and adjustment procedures are not described. The record therefore does not support detailed conclusions about which participant or dosing circumstances are represented by the pooled group summaries. These are reporting limitations, not proof that the trial itself lacked the relevant procedures.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Efficacy and Safety of Nebivolol (Added to Lisinopril or Losartan) in Hypertensive Patients — NCT00734630.
• Registry record last updated 2011-04-26; status last verified 2011-03.
• Results first posted 2011-04-26.
• 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

The registry record describes a completed Phase 4, randomized, double-blind, placebo-controlled, parallel-group study of nebivolol added to lisinopril or losartan in patients with hypertension. Enrollment is listed as 491, with study start 2008-08 and primary completion 2010-03. The primary endpoint was change from baseline in mean seated trough cuff systolic blood pressure at Week 12, using LOCF. A diastolic blood-pressure change at Week 12 was posted as a secondary outcome.

The primary arm summaries show reductions in both groups. The unadjusted recalculated mean difference is -2.8 mmHG, with a 95% interval that includes zero and a p-value of 0.059. The secondary comparison is directionally consistent, but it is unadjusted and the registry does not report a multiplicity plan. Missing-data details, the analysis population, the original sample-size justification, and the sponsor’s statistical analysis are not reported in the registry record.