Efficacy of Losartan + Amlodipine Compared to Amlodipine Alone in the Treatment of Uncontrolled High Blood Pressure (MK-0954F-399): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Efficacy of Losartan + Amlodipine Compared to Amlodipine Alone in the Treatment of Uncontrolled High Blood Pressure (MK-0954F-399) (NCT01277822), a randomized phase 4 study. The primary outcome is Change in Mean Sitting Diastolic Blood Pressure (MSDBP) at Week 8.

2. Clinical Question

This is a comparison of two assigned treatment regimens over a defined treatment period, not a comparison with no treatment. The principal posted result describes the average change in diastolic pressure in each arm and the difference between those changes. Those summaries help show the direction and size of the observed changes, but they do not by themselves establish whether a prespecified non-inferiority criterion was met.

The registry lists 334 participants enrolled. The primary endpoint results include 162 participants in the combination arm and 160 in the amlodipine arm. These analysis counts are not the same as the full enrollment figure; the registry’s Full Analysis Set definition and the results tables specify which participants contributed to the endpoint analysis. Reasons why some enrolled participants do not appear in those endpoint counts are not reported in the registry record.

3. Trial Design

This was a Phase 4, randomized, double-blind, parallel-group clinical study in participants with hypertension. The registry describes an eight-week comparison of losartan/amlodipine 100/5 mg combination treatment with amlodipine 10 mg monotherapy. Participants were assigned to one of the two treatment regimens, and matching placebo tablets were used in each arm. The study is marked completed in the registry record.

The primary endpoint was change in mean sitting diastolic blood pressure from baseline to Week 8. The registry also lists seven secondary outcomes, including blood-pressure measures at Week 4, systolic blood pressure at Week 8, target blood-pressure attainment, peripheral edema, and change in ankle circumference. Results are posted for only some of the listed secondary outcomes; the remaining listed outcomes are not reported in the registry record.

The primary endpoint analysis population was the Full Analysis Set. It included randomized participants who took at least one dose of study drug and had blood-pressure measurements at baseline and at least one post-randomization visit. The primary results table contains 162 participants in the combination group and 160 in the amlodipine group. The Week 4 secondary blood-pressure analyses contain 156 participants in each arm. These varying counts indicate that the endpoint summaries are based on the participants included in the corresponding results, but the reasons for the differences are not reported in the registry record.

The registry describes a t-test, two-sided, for the sponsor’s posted primary comparison, with mean difference in final values as the parameter. It labels that analysis as a legacy non-inferiority or equivalence analysis. The planned non-inferiority margin, the full statistical analysis plan, and the original sample-size assumptions are not reported in the registry record. The record also does not report whether interim analyses were planned or conducted. The posted results therefore allow a description of the treatment groups and available endpoint estimates, but not a full audit of the original design and analysis decisions.

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: Full Analysis Set defined as all participants who were randomized, took at least 1 dose of study drug, and had blood pressure measurements at baseline and at least 1 post-randomization blood pressure measurement.

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 Change in Mean Sitting Diastolic Blood Pressure (MSDBP) at Week 8, measured over Baseline and Week 8.

The primary endpoint is the change in mean sitting diastolic blood pressure from baseline to Week 8, measured in mmHg. Diastolic pressure is the lower blood-pressure reading, and the endpoint summarizes how the group average changed over the treatment period. A negative change in the posted results represents a decrease from baseline. The endpoint is continuous: each participant’s measurement contributes to a group mean rather than being reduced to a yes-or-no outcome.

According to the registry description, blood pressure was measured while the participant was seated, using an automated sphygmomanometer. Three readings were taken at two-minute intervals, and their average was recorded. Averaging repeated readings is a way to represent a measurement session while reducing reliance on any single reading. This is a general measurement principle; the registry does not provide further details about measurement standardization or device calibration.

A mean change is useful for comparing the average response in randomized groups, while the standard deviation describes the spread of individual changes around each group mean. Neither one alone describes every participant’s outcome. The primary endpoint was measured at Week 8, providing a summary at the end of the stated treatment period. It does not, on its own, describe what happened after treatment ended or establish the longer-term pattern.

The registry’s summary states that the study was intended to assess non-inferiority. For that purpose, the size and direction of the difference must be judged against a prespecified margin and a defined analysis rule. Those details are not reported in the registry record, so the endpoint estimates can be described, but the non-inferiority decision cannot be independently verified from the record alone.

7. Results Posted in the Registry

• Amlodipine: mean -8.80 versus -10.10 on control; difference 1.30 (95% CI -0.38 to 2.98), standardized effect d = 0.17; z-test p = 0.130.

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.

Change in Mean Sitting Diastolic Blood Pressure (MSDBP) at Week 4

• 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:
  • Amlodipine: mean -10.00 versus -9.30 on control; difference -0.70 (95% CI -2.44 to 1.04), standardized effect d = -0.09; z-test p = 0.431.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Amlodipine and the control. The interval gives the range of effects that remain compatible with the data.

Change in Mean Sitting Systolic Blood Pressure (MSSBP) at Week 8

• 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:
  • Amlodipine: mean -12.70 versus -15.00 on control; difference 2.30 (95% CI -0.19 to 4.79), standardized effect d = 0.20; z-test p = 0.071.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Amlodipine and the control. The interval gives the range of effects that remain compatible with the data.

Change in Mean Sitting Systolic Blood Pressure (MSSBP) at Week 4

• 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:
  • Amlodipine: mean -12.30 versus -12.50 on control; difference 0.20 (95% CI -2.49 to 2.89), standardized effect d = 0.02; z-test p = 0.884.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Amlodipine and the control. The interval gives the range of effects that remain compatible with the data.

The secondary results add context on other blood-pressure measures and time points, as well as target attainment and safety-related outcomes listed in the registry. Among the posted blood-pressure summaries, changes in systolic and diastolic pressure are described for Week 4 and Week 8. Their group comparisons vary in direction and apparent separation. That variation is a reason to read the secondary outcomes as a set of supporting descriptions rather than as a single uniform pattern.

The primary endpoint remains the Week 8 change in mean sitting diastolic pressure. Secondary results do not replace it, and findings on related measures are not independent confirmations when they come from the same participants and study. They can help show whether the broad pattern is similar across related measurements, but the registry does not report a hierarchy that would make any particular secondary endpoint confirmatory.

The registry lists seven secondary outcomes, while the posted secondary results cover only a subset. The outcomes not represented in the posted numerical summaries are not reported in the registry record. This limits how comprehensively the secondary outcome family can be assessed from the available record.

The secondary analyses include unadjusted comparisons. General explanation: when many outcomes and time points are tested, some results may look more striking by chance, even when there is no systematic difference. Adjusting for multiplicity or defining an outcome hierarchy can address this issue, but the registry does not report such an approach. Consequently, nominal secondary p-values should carry less weight than a prespecified, multiplicity-controlled primary analysis. They are best treated as exploratory context, not as stand-alone proof of a treatment effect or of equivalence.

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

• Change in Mean Sitting Diastolic Blood Pressure (MSDBP) at Week 4
• Change in Mean Sitting Systolic Blood Pressure (MSSBP) at Week 8
• Change in Mean Sitting Systolic Blood Pressure (MSSBP) at Week 4
• Percentage of Participants Who Achieve Target Blood Pressure at Week 8
• Percentage of Participants Who Achieve Target Blood Pressure at Week 4
• Percentage of Participants Who Had Peripheral Edema During the Study
• Change From Baseline in Ankle Circumference at Week 8

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is a continuous measurement summarized by a mean and standard deviation in each arm. The mean describes the group average change from baseline, while the standard deviation describes the variation among participant measurements around that average. A group mean can be useful for comparing randomized arms, but it does not imply that every participant experienced a change close to the mean.

The sponsor’s posted primary analysis is described as a two-sided t-test comparing final values, with a mean difference reported. A t-test is a general method for assessing whether group means differ, taking account of the variation and amount of data in the groups. A two-sided test considers departures in either direction. The registry does not provide enough detail to reconstruct every aspect of the sponsor’s calculation or its full statistical model, so the posted result should be treated as the sponsor’s reported analysis rather than as a fully auditable analysis plan.

The page also shows a recalculation from the posted arm-level means, standard deviations, and sample sizes. This is a simple, unadjusted comparison of the summary statistics, rather than a reproduction of any unreported participant-level model. It provides a transparent way to relate the displayed group summaries to a difference estimate and uncertainty interval. Small differences between a recalculation and the sponsor’s estimate can arise when the analyses use different definitions or methods; the registry does not supply enough detail to determine all such reasons. The recorded discrepancy flag is false.

A confidence interval gives a range of values that are compatible with the data under the analysis method and its assumptions. In repeated use of the same method, intervals constructed this way have a stated coverage property. It is not a range containing a known fixed proportion of individual participants, and it is not a guarantee that the true effect lies inside the interval. For this trial, the sponsor’s primary 95% confidence interval is reported as -3.0 to 0.4 for the sponsor’s direction of subtraction. The recalculated interval is shown in the associated results display.

The p-value and confidence interval answer related but different questions. The p-value summarizes the data’s compatibility with a null difference under a test; the interval conveys a set of plausible effect estimates and their precision. Neither should be interpreted alone as a measure of clinical importance. A small p-value does not establish that an effect matters clinically, and a larger p-value does not show that the groups are equivalent. Equivalence and non-inferiority require their own prespecified margins and decision rules.

That distinction matters because the registry summary describes a non-inferiority objective, and the sponsor analysis is labelled as a legacy non-inferiority or equivalence analysis. General explanation: a non-inferiority assessment asks whether the comparison excludes an unacceptable loss relative to a chosen margin. The margin is a design choice that must be stated before interpreting the result. It is not reported in the registry record. Without it, readers cannot tell whether the sponsor’s interval satisfies the intended criterion, even though the reported interval and test are available.

General explanation: over-dispersion is a concern when outcome variability is greater than the model assumes. It is especially relevant to count outcomes, where a model that assumes a particular count distribution may understate uncertainty if the data are more variable. The posted primary endpoint is a continuous blood-pressure measure analyzed as a mean, and the registry does not report a count model or an over-dispersion assessment. This concept should not be mistaken for a reported feature of this trial’s analysis.

The primary analysis population is described as the Full Analysis Set, with a defined requirement for randomization, treatment exposure, and blood-pressure measurements. This is the population attached to the posted primary endpoint results. General explanation: the analysis population determines which randomized participants contribute to an estimate, and different inclusion rules can affect interpretation. The registry does not report a complementary per-protocol analysis, a detailed missing-data method, or how participants without endpoint measurements were handled beyond the stated population definition.

Multiplicity is the issue created when many outcomes or tests are assessed. General explanation: as the number of tests increases, the chance of seeing at least one apparently notable result by chance can rise. The registry lists several secondary outcomes and reports analyses for some of them, but does not report a multiplicity adjustment or a prespecified hierarchy among outcomes. The secondary p-values should therefore be read as unadjusted evidence rather than as confirmatory conclusions.

The design labels and endpoint summaries do not reveal whether the trial used interim analyses, how the original target enrollment was chosen, or what assumptions informed the planned power. Those details are not reported in the registry record. The planning illustrations elsewhere on this page are separate calculations based on the observed effect and stated illustrative assumptions. They are not descriptions of the trial’s original design.

11. Confidence Intervals and Precision

The precision of a treatment comparison is conveyed chiefly by its confidence interval. A narrow interval indicates that the estimate is more tightly constrained under the analysis assumptions; a wide interval leaves more room for different underlying effects. The sponsor’s primary interval is 95% and runs from -3.0 to 0.4 in the sponsor’s reported direction. It crosses zero, so it includes no difference as well as differences in either direction.

The recalculated estimate is reported in the opposite subtraction order, amlodipine minus combination treatment. Its interval is displayed with the recalculation and also includes no difference. Keeping the direction of subtraction in mind is important: reversing the order changes the sign of the difference, while the underlying contrast is the same comparison. The two arm means alone do not show how precisely their difference is estimated; the interval is needed for that.

The standard deviations in the primary results are 7.6 mmHg and 7.8 mmHg, with 162 and 160 participants in the respective endpoint groups. These values indicate that participant-level changes varied around the group means. They also help explain why the group-average contrast has uncertainty: a mean difference is estimated from finite groups with individual variation, not observed without error.

Precision is not the same as importance. Even a precise estimate would need clinical and design context, while an imprecise estimate can leave multiple interpretations consistent with the data. Here, the registry does not report the non-inferiority margin, so readers cannot assess the interval against the criterion that would be central to the stated study objective. The confidence interval is informative about uncertainty in the difference, but it cannot supply an unreported decision threshold.

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 is a planning illustration derived from the observed effect; it is not a record of the study’s original enrollment calculation. The listed figures are participants per arm, not total participants and not total events. The assumptions stated for this illustration are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. It considers the effect to detect at the stated fraction of the observed effect.

The 80% power column describes the number of participants per arm that the illustration estimates would be needed to have an 80% chance of detecting the specified effect under those assumptions, if that effect were the true one. The 90% power column gives the corresponding planning figure for a higher chance of detection. These are prospective design quantities, not a measure of how much power the completed trial had after its results were observed. This is not observed power.

Rows describe planning for the full observed effect, 75% of the observed effect, and 50% of the observed effect. A smaller effect is harder to distinguish from random variation, so the illustration requires more participants for the smaller-effect scenarios. The results are specific to the observed summary effect and the stated calculation assumptions; they should not be treated as the sample-size justification used by the sponsor.

The registry does not report the original sample-size calculation, its assumed treatment difference, the non-inferiority margin, or the design assumptions used to set enrollment. The planning table and curve help readers see how required sample size changes under the displayed scenarios, but they cannot establish whether the trial’s original design was adequate for its stated objective.

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 = 1.300; pooled standard deviation σ = 7.700.
2. n = 2 × (1.96 + 0.842)² × 7.700² / 1.300² = 550.7, rounded up to 551 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 <- 1.3                      # observed difference in means
sigma <- 7.70002435061085                     # 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(1277822)
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 = 551 (80% power), 738 (90% power)
 75% of observed effect: n per arm = 980 (80% power), 1,311 (90% power)
 50% of observed effect: n per arm = 2,203 (80% power), 2,950 (90% power)
power.t.test: 551.7 
Simulated power at n = 551 per arm: 0.799 (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. Analyses Reported by the Sponsor

The sponsor’s primary result reports a two-sided t-test for mean difference in final values and a 95% confidence interval from -3.0 to 0.4. The posted analysis is labelled as a legacy non-inferiority or equivalence analysis. The registry’s label identifies the broad analysis context, but it does not give the non-inferiority margin or full decision rule. That information is necessary to decide whether the sponsor’s result meets a non-inferiority criterion.

The recalculation uses the posted arm-level change means, standard deviations, and sample sizes to make a simple unadjusted comparison. It expresses the difference as amlodipine minus combination treatment, whereas the sponsor’s estimate is reported in the reverse direction. The signs therefore differ, but the estimates describe the same two arms with opposite subtraction orders. The recalculated unadjusted p-value is 0.13; the sponsor reports a two-sided p-value that is close to this value.

The recalculation is not a replacement for the sponsor’s analysis. It does not use participant-level data, and it cannot reproduce unreported model details or analysis choices. The record’s discrepancy indicator is false, but the calculations still answer slightly different questions: one is a summary-statistic recalculation of change scores, and the sponsor’s reported parameter is a mean difference in final values. The sponsor’s posted analysis remains the trial’s reported analysis; the recalculation is a check on the broad pattern visible in the summary data, not independent verification of the original analysis plan.

15. Multiplicity, Missing Data and Analysis Populations

The registry reports a primary endpoint and several secondary outcomes, with analyses posted for a subset of the latter. It does not report a multiplicity adjustment, a testing hierarchy, or a plan for deciding which secondary results would be confirmatory. That omission matters because multiple tests can produce apparently noteworthy results by chance. General explanation: a prespecified hierarchy or statistical adjustment can control how evidence is interpreted across a family of outcomes. Without a reported approach, the secondary tests should be regarded as unadjusted and interpreted cautiously.

The registry gives the primary analysis population definition: randomized participants who took at least one dose and had a baseline blood-pressure measure and at least one post-randomization measure. It does not report a detailed flow of participants from enrollment through each analysis, reasons for exclusion from endpoint summaries, or a separate per-protocol population. The primary table includes fewer participants than the enrollment total, and the record does not explain the full accounting for that difference.

The missing-data method is not reported in the registry record. The definition of the Full Analysis Set does not, by itself, explain how missing Week 8 values were handled, whether any values were imputed, or what assumptions were made about missingness. These issues can affect an estimate when endpoint data are unavailable, particularly for a non-inferiority objective, but the record does not provide enough information to assess their effect.

The original statistical analysis plan, interim-analysis arrangements, and sample-size justification are also not reported. The posted sponsor test and its legacy analysis label provide some information about the reported comparison, but they are not a substitute for the complete planned methods. In particular, the non-inferiority margin and decision rule are absent. Readers can describe the posted effect estimates and intervals, but cannot determine from the registry record how those results relate to the full prespecified analysis strategy.

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: accidental overdose (1.8%), asthenia (0.6%), excoriation (0.6%), facial bones fracture (0.6%), fracture (0.6%).

The registry lists serious adverse events for 6 of 168 participants in the losartan 100 mg/amlodipine 5 mg group and 5 of 166 participants in the amlodipine 10 mg group. For other adverse events, the posted counts are 6 of 168 and 11 of 166, respectively. These are descriptive counts for the groups shown in the safety table; they should not be interpreted as adjusted comparisons or as proof that treatment caused or prevented an event.

The listed serious-event terms include accidental overdose at 1.8%, and asthenia, excoriation, facial bones fracture, fracture, and dizziness at 0.6% each. These entries describe terms reported in the registry, not a complete clinical assessment of each event or its relationship to treatment. The death fields contain no numerical count; deaths are not reported in the registry record.

Safety counts can be affected by the duration of observation, event definitions, and how events were collected. The trial’s stated treatment period was eight weeks, and the registry record does not provide enough detail to make broader comparisons beyond the posted counts. Small differences in counts should not be treated as evidence of a safety advantage or disadvantage on their own.

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

The posted results show average decreases in sitting diastolic blood pressure in both randomized groups over the eight-week period. The Week 8 mean change was -10.1 mmHg for losartan/amlodipine and -8.8 mmHg for amlodipine. The estimated difference is small relative to the variation shown in the groups, and the confidence interval includes no difference. The result describes the data and their uncertainty; it does not establish that one regimen is better or that the regimens are equivalent.

The registry frames the trial as a non-inferiority study. Non-inferiority is not established merely because a conventional test does not show a statistically significant difference. It requires a prespecified margin and a confidence interval that satisfies the design’s decision rule. The margin and the full decision rule are not reported in the registry record. The sponsor’s reported interval can therefore be presented, but the non-inferiority conclusion cannot be independently determined from this record alone.

The results concern group averages in the analysis population and the endpoint measurement at Week 8. They do not describe every participant’s response, outcomes beyond the treatment period, or effects on other health outcomes not reported in the results. A change in a blood-pressure measurement is not itself a complete account of benefits and harms.

The sample-size illustrations elsewhere on the page are not evidence about the trial’s observed power and do not explain the original enrollment target. They are based on the observed effect under stated planning assumptions. Likewise, the unadjusted secondary analyses offer context but do not resolve the primary endpoint’s uncertainty, particularly when no multiplicity strategy is reported.

In short, the available record supports a careful description of the observed group means, comparison, and uncertainty. It does not support claims beyond those measurements and the stated study period, and key information needed to assess the original non-inferiority objective is absent.

18. Why This Trial Matters Statistically

This trial illustrates why a difference estimate and its uncertainty are more informative than a simple statement that a comparison was or was not statistically significant. The arm means show changes in both groups, while the interval shows that the estimated between-group contrast remains uncertain. Readers can see the direction and scale of the observed comparison without treating a single p-value as a complete interpretation.

It also demonstrates a central feature of non-inferiority research: the decision depends on a prespecified margin, not merely on whether a conventional test detects a difference. The registry identifies the study as intended to address non-inferiority, but the margin and full decision rule are not reported. That gap prevents readers from independently evaluating the key design question, even though the sponsor’s estimate and interval are posted.

The page separates the sponsor’s reported analysis from a simple recalculation based on group summaries. This distinction is useful for statistical literacy. A summary-based calculation can check the broad numerical pattern and make the contrast easier to inspect, but it cannot reproduce unreported participant-level methods or replace the sponsor’s analysis.

Finally, the secondary endpoints and planning illustrations show why context matters. Multiple secondary tests need cautious interpretation when no multiplicity plan is reported, and planning figures based on an observed effect are not the same as the original sample-size rationale. Together, these features make the record a useful example of reading effect estimates, uncertainty, analysis labels, and reporting gaps without drawing conclusions beyond the information available.

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.

The registry record does not report the non-inferiority margin or the complete decision rule, even though the study summary describes a non-inferiority objective and the sponsor analysis carries a non-inferiority or equivalence label. This is a central limitation for interpreting the primary comparison. The reported confidence interval can be described, but without the margin readers cannot judge whether it meets the intended criterion.

The record also does not report the original sample-size justification, the full statistical analysis plan, or whether interim analyses were planned or conducted. The planning illustrations on this page use the observed effect and stated assumptions; they cannot fill in those missing design details. The reported primary analysis is a two-sided t-test for final values, but the record does not give enough information to reconstruct every analysis choice.

Although the primary population definition is stated, the registry does not provide a detailed participant flow or explain why the endpoint counts differ from total enrollment. Missing-data handling is not reported, and there is no posted per-protocol analysis in the information. Those gaps are relevant when assessing a non-inferiority result, where choices about analysis populations and missing observations can influence interpretation.

The secondary results are incomplete relative to the outcomes listed, and the registry does not report a multiplicity adjustment or outcome hierarchy. The secondary findings should therefore be treated as descriptive support rather than confirmatory evidence. Safety information is also limited to the posted event counts and terms; deaths are not reported in the registry record, and the available information does not establish causal relationships.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Efficacy of Losartan + Amlodipine Compared to Amlodipine Alone in the Treatment of Uncontrolled High Blood Pressure (MK-0954F-399) — NCT01277822.
• Registry record last updated 2024-06-20; status last verified 2022-02.
• Results first posted 2014-04-24.
• 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

This completed Phase 4 randomized, double-blind, parallel-group study compared once-daily losartan/amlodipine 100/5 mg with amlodipine 10 mg over eight weeks in participants with hypertension who had not appropriately responded to amlodipine 5 mg monotherapy. The primary endpoint was change in mean sitting diastolic blood pressure from baseline to Week 8.

The primary group means were -10.1 mmHg and -8.8 mmHg, with a recalculated difference of 1.3 mmHg in the amlodipine-minus-combination direction. The sponsor posted a two-sided analysis with a 95% confidence interval from -3.0 to 0.4 in the reverse direction. The record does not report the non-inferiority margin, original sample-size rationale, full analysis plan, or missing-data method, limiting independent evaluation of the stated non-inferiority objective.