Efficacy and Safety of Valsartan Versus Amlodipine in Postmenopausal Women With Hypertension: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Efficacy and Safety of Valsartan Versus Amlodipine in Postmenopausal Women With Hypertension (NCT00171054), a randomized phase 4 study. The primary outcome is Change From Baseline to Week 38 in the Carotid-femoral Pulse Wave Velocity (PWV).

2. Clinical Question

The clinical question was not limited to blood pressure. The registry identifies arterial properties, including pulse wave velocity, as a focus, and lists additional measures of vascular function and distensibility. The primary comparison concerns estimated mean change in pulse wave velocity, rather than the proportion of participants crossing a threshold or experiencing a clinical event. A negative change in each group’s estimate indicates a decline from baseline on the measured scale; the between-group estimate addresses whether the average changes differed.

The registry describes the study as randomized, double-blind, parallel-group, and active-controlled. The posted primary estimates were -1.9 m/s for valsartan and -1.7 m/s for amlodipine. The estimated difference, expressed as amlodipine minus valsartan, was 0.2 m/s. The confidence interval for that difference extends in both directions around zero, and the unadjusted p-value is 0.632. These results do not establish a clear difference between the groups in the primary measure; they also do not establish that the treatments are equivalent.

3. Trial Design

The registry describes a Phase 4, randomized, parallel-group study with active control and quadruple masking. The official title calls it a 38-week study. Enrollment was 125, and the listed condition was hypertension. The study status is completed. The registry lists Novartis as sponsor, a start date of 2003-09, and primary completion in 2007-10.

The comparison was between valsartan 320 mg and amlodipine 10 mg. The brief summary says each could be used with the possible addition of hydrochlorothiazide. The registry lists hydrochlorothiazide as an intervention, but the arm descriptions are blank, so the precise use of this additional drug and any treatment adjustments are not reported in the registry record. The record’s quadruple-masking label does not identify the masked roles in the information available for this analysis.

Randomization is intended to make the comparison between groups less vulnerable to systematic differences at the start of a trial. An active-controlled design compares the study treatments with one another, rather than with an untreated or placebo group. A parallel-group design assigns participants to a group that is followed separately. These are general features of the design; they do not by themselves establish that all potential sources of bias were avoided.

The primary endpoint was change from baseline to Week 38 in carotid-femoral pulse wave velocity. The defined primary analysis population required a baseline measure and at least one post-baseline measure, not necessarily a Week 38 measure. Group estimates were reported as least-squares means with standard errors. The registry does not report the original sample-size justification, detailed allocation procedures, the identities of those masked, or the full statistical analysis plan. The enrollment figure is not itself evidence about how the target sample size was chosen.

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: Intent-to-treat. The intent to treat population is defined as those who provide a baseline measure and at least one post-baseline measurement (not necessarily an endpoint measure)

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 From Baseline to Week 38 in the Carotid-femoral Pulse Wave Velocity (PWV), measured over Baseline and Week 38.

The primary endpoint was change from baseline to Week 38 in carotid-femoral pulse wave velocity (PWV), measured in m/s. PWV describes the speed of the pressure wave traveling along an arterial path. In general, arterial stiffness can influence this speed, which is why PWV is used as a vascular measure; it is not itself a direct measure of a clinical event.

The registry describes measurement using transcutaneous Doppler flow recordings and the foot-to-foot method, with timing triggered by a simultaneous electrocardiogram. Doppler tracings were taken at the left common carotid artery and the right femoral artery. The time delay between the ECG R wave and the base of the recorded flow waves was averaged over 10 beats. Distance was measured over the body surface from the suprasternal notch to the carotid artery. PWV was calculated as distance divided by time, expressed in the record as PWV=D/t.

Change from baseline focuses the comparison on the amount of change over follow-up rather than only on the endpoint value. Comparing group means can summarize the average change, but it does not show the distribution of individual responses or how many participants had a particular response. The endpoint is a continuous measure, so the posted estimates and their uncertainty should be interpreted on the m/s scale. The registry reports least-squares means, but further details about the adjustment model are not reported in the registry record.

7. Results Posted in the Registry

• Amlodipine 10 mg: mean -1.70 versus -1.90 on control; difference 0.20 (95% CI -0.62 to 1.02), standardized effect d = 0.09; z-test p = 0.632.

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 From Baseline in Post-ischemic Forearm Skin Reactive Hyperemia 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 errors.
• Result:
  • Amlodipine 10 mg: mean -105.60 versus 25.40 on control; difference -131.00 (95% CI -172.84 to -89.16), standardized effect d = -1.19; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Amlodipine 10 mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Change From Baseline in Post-ischemic Forearm Skin Reactive Hyperemia at Endpoint (Week 38)

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard errors.
• Result:
  • Amlodipine 10 mg: mean -94.60 versus -9.70 on control; difference -84.90 (95% CI -123.61 to -46.19), standardized effect d = -0.83; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Amlodipine 10 mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Change From Baseline for Endothelial Function Measured by Brachial Artery Flow-mediated Vasodilatation (FMD) Using the Brachial Artery Reactivity Test (BART) 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 errors.
• Result:
  • Amlodipine 10 mg: mean -8.60 versus -8.70 on control; difference 0.10 (95% CI -0.91 to 1.11), standardized effect d = 0.04; z-test p = 0.847.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Amlodipine 10 mg and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes cover several aspects of vascular function: post-ischemic forearm skin reactive hyperemia, brachial artery flow-mediated vasodilatation, and carotid distensibility. Some outcomes were specified at Week 12 and at Week 38. The pattern in the reported results is not uniform across these types of measures: the hyperemia comparisons show sizeable contrasts in the posted estimates, while the Week 12 FMD estimates are close together and its comparison interval spans zero. These outcomes measure different physiological properties, so they need not move in parallel with PWV.

The primary result remains the result for change in carotid-femoral PWV. Secondary findings may add context about other vascular measurements, but they do not substitute for the primary comparison or directly establish a difference in PWV. Conversely, a primary result without a clear between-group difference does not mean that every secondary measure must show the same pattern. The registry names further secondary measures, including Week 38 FMD and carotid distensibility, but their results are not reported in the registry record.

Unadjusted secondary results carry less weight because multiple outcomes and time points create more opportunities for apparently notable findings by chance. In general, a multiplicity plan can control the overall error rate or specify which comparisons are confirmatory. The registry record does not report such a plan or a multiplicity-adjusted analysis. The secondary p-values should therefore be read as individual, unadjusted comparisons, not as definitive evidence across the full set of vascular outcomes. This caution concerns the strength of inference, not whether the posted estimates should be described.

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

• Change From Baseline in Post-ischemic Forearm Skin Reactive Hyperemia at Week 12
• Change From Baseline in Post-ischemic Forearm Skin Reactive Hyperemia at Endpoint (Week 38)
• Change From Baseline for Endothelial Function Measured by Brachial Artery Flow-mediated Vasodilatation (FMD) Using the Brachial Artery Reactivity Test (BART) at Week 12
• Change From Baseline for Endothelial Function Measured by Brachial Artery Flow-mediated Vasodilatation (FMD) Using the Brachial Artery Reactivity Test (BART) at End-point (Week 38)
• Changes in Mean Left Carotid Distensibility at Week 12
• Changes in Mean Left Carotid Distensibility at Week 38
• Changes in Mean Right Carotid Distensibility at Week 12
• Changes in Mean Right Carotid Distensibility at Week 38

9. Statistical Interpretation

10. Statistical Methods Explained

What does the group estimate represent?

The primary outcome is continuous, so the registry reports a mean change for each treatment group. The values are identified as least-squares means. In general, a least-squares mean is a model-based estimate of a group mean, often adjusted for terms in an analysis model. The model terms and adjustment details are not reported in the registry record, so the posted estimates cannot be described as adjusted for any particular baseline variable or other factor.

The estimated primary changes were -1.9 m/s for valsartan and -1.7 m/s for amlodipine. Each estimate summarizes the group average on the outcome scale; neither describes every participant’s change. A group mean can conceal a range of individual values, and the registry summary does not provide individual-level results or a distributional description. The number reported beside each group estimate is a standard error, not a standard deviation. A standard deviation describes variability among measurements, while a standard error describes uncertainty in an estimated mean.

How should the comparison be read?

The reported comparison is a mean difference of 0.2 m/s, with amlodipine compared against valsartan. In general, a difference estimate expresses the direction and size of the contrast on the outcome’s original scale. A value of zero corresponds to no difference between the two estimated means. The confidence interval spans values below and above zero, so it does not isolate one direction of difference. The unadjusted p-value is 0.632. In general, a p-value measures how unusual data at least as incompatible with a specified null hypothesis would be if that hypothesis and the analysis assumptions held. It is not the probability that the null hypothesis is true, and it is not a measure of clinical importance.

The comparison is labelled unadjusted. That means the p-value should not be read as accounting for the number of outcomes or comparisons examined. The record does not report a multiplicity correction for this result. The posted comparison can help describe the primary contrast, but the record does not include enough detail to reproduce a full model-based analysis independently.

Why does the confidence interval matter?

In general, a confidence interval communicates the precision of an estimate by giving a range of values that are reasonably compatible with the data and the method’s assumptions. A narrower interval indicates greater precision than a wider interval on the same scale. For this primary comparison, the interval includes zero and extends in both directions. It therefore allows uncertainty about both the direction and size of the difference. It does not establish that the groups are equivalent; an equivalence conclusion would require a prespecified margin and an analysis designed for that question, neither of which is reported in the registry record.

Standard errors and confidence intervals are related but are not interchangeable descriptions. The group standard errors quantify uncertainty around each reported mean, while the comparison interval quantifies uncertainty around the difference. The comparison interval is the more direct tool for judging precision of the treatment contrast. The registry’s group estimates and standard errors are posted as summary statistics, and the recalculated contrast should be understood as an unadjusted re-calculation from those summaries.

What assumptions affect a recalculation?

Recalculated comparisons based on summary statistics necessarily rely on assumptions about how those summaries relate to the underlying observations. In general, standard-error-based methods may use a normal approximation, and a pooled estimate of variability can be used for a standardized comparison or planning illustration. Such calculations are not equivalent to reproducing the original participant-level model. The registry does not report the detailed model, covariance structure, treatment of baseline values, missing-data method, or any adjustments used for the primary analysis. Those details are therefore not inferred.

Over-dispersion is a general concern when observed variation is greater than assumed by a statistical model: uncertainty may then be understated if the model does not account for that extra variation. Conversely, assumptions that are too conservative can make uncertainty appear larger. The registry record does not report a dispersion assessment for this outcome, so no claim can be made about whether over-dispersion was present. More broadly, the appropriateness of a model depends on the outcome, design, missingness, and data structure, not only on the reported group means.

What does the analysis population include?

The registry defines the intent-to-treat population as participants with a baseline measure and at least one post-baseline measure, which need not be the endpoint measure. This definition is therefore narrower than simply all randomized participants and does not require that the Week 38 outcome be available. The record does not explain how participants with some, but not all, measurements contributed to the endpoint estimate, or how missing values were handled. The label alone should not be taken as evidence that every randomized participant was included in the primary analysis.

These methods concepts are general explanations of the reported statistics. Details such as the primary model specification, assumptions checks, handling of missing data, and planned multiplicity strategy are not reported in the registry record. The estimates can be interpreted as posted group summaries and a summary-based comparison, while the absence of those details limits assessment of how closely that comparison reflects the original analysis plan.

11. Confidence Intervals and Precision

The estimated primary difference was 0.2 m/s, and its confidence interval extends across zero. This means the data do not pin down a single direction of difference: values favoring either group remain compatible with the interval. The interval is also wide enough that the estimate should not be treated as proof that the groups have the same mean change. Equivalence requires a defined margin and an analysis designed to test equivalence, neither of which is reported in the registry record.

A confidence interval is a range generated by a statistical method to express uncertainty around an estimate. In general, a narrower interval indicates greater precision, assuming the same scale and method. For this comparison, the interval is more informative about precision than the point estimate alone. The point estimate is close to zero, but that proximity does not remove the uncertainty represented by the interval.

The standard errors for the group estimates were 0.29 m/s for valsartan and 0.3 m/s for amlodipine. These quantify uncertainty in the estimated group means; they are not the standard deviations of individual outcomes. The registry reports no confidence limits for the separate group estimates, while the comparison interval is available from the summary-based recalculation. The recalculated interval should not be mistaken for an adjusted sponsor analysis. The registry does not report a separate sponsor comparison that would permit direct comparison with it.

Precision is distinct from clinical importance. The registry record does not report a threshold defining a meaningful difference in PWV, so the interval cannot be classified against such a threshold. It also cannot be used to infer precision for clinical events or outcomes not measured by the primary endpoint.

12. Planning a Similar Trial: Sample Size

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

The planning figures are participants per arm, not total events. They are illustrations based on the observed effect, rather than the trial’s original design assumptions. The stated assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation; each planning scenario uses the stated fraction of the observed effect as the effect to detect. The original trial’s sample-size justification is not reported in the registry record.

The 80% power column gives the estimated participants per arm for a hypothetical study to have an 80% chance of detecting the specified effect under those assumptions, if the effect and assumptions are correct. The 90% power column describes the corresponding planning target for a 90% chance. These are design calculations, not probabilities that the current result is correct. For the primary outcome, planning for 100% of the observed effect gives 1,860 participants per arm for 80% power and 2,490 participants per arm for 90% power. Planning for 75% of the observed effect gives 3,307 and 4,427 participants per arm, respectively; planning for 50% gives 7,440 and 9,959.

Smaller effects are harder to distinguish from random variation, so the planning requirement rises as the target effect becomes smaller. The displayed figures should be read as conditional illustrations, not as a recommended design or a reconstruction of the actual protocol. In particular, observed differences can be unstable, and using an observed effect as a planning target does not establish that the same effect would recur in another study. This is not observed power.

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 = 0.200; pooled standard deviation σ = 2.177.
2. n = 2 × (1.96 + 0.842)² × 2.177² / 0.200² = 1,859.8, rounded up to 1,860 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 <- 0.2                      # observed difference in means
sigma <- 2.17691370316511                     # 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(171054)
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 = 1,860 (80% power), 2,490 (90% power)
 75% of observed effect: n per arm = 3,307 (80% power), 4,427 (90% power)
 50% of observed effect: n per arm = 7,440 (80% power), 9,959 (90% power)
power.t.test: 1860.7 
Simulated power at n = 1,860 per arm: 0.801 (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 lists a primary endpoint and multiple secondary outcomes, including measurements at different follow-up times. When many outcomes or comparisons are examined, the chance of at least one apparently unusual result can increase. In general, multiplicity procedures address this issue by adjusting significance thresholds or by arranging outcomes in a prespecified testing hierarchy. The registry record does not report whether such a procedure was planned or used, and the available secondary comparisons are identified as unadjusted.

That absence matters most when interpreting secondary p-values. An unadjusted result can describe the evidence for one comparison under its own test, but it does not account for the broader set of comparisons. The primary comparison is also reported with an unadjusted p-value. No multiplicity-adjusted primary result or testing hierarchy is reported in the registry record. This does not make the estimates unusable; it limits claims based on statistical significance across multiple outcomes.

The primary population definition requires a baseline measure and at least one post-baseline measure, not necessarily a Week 38 measurement. The registry does not state how missing Week 38 values were handled, whether any imputation was used, how participants with incomplete follow-up contributed, or whether sensitivity analyses assessed the impact of missing data. It is therefore not possible to assess from the registry record whether the missing-data assumptions are plausible or how robust the primary estimate is to alternative assumptions.

The record also does not report a full analysis plan, the primary model specification, interim analyses, or details of any protocol deviations. The definition of the analysis population is available, but the label intent-to-treat should not be taken to mean that all randomized participants necessarily contributed to the primary estimate. More detail about analysis populations, missingness, and prespecified multiplicity handling would help readers judge the confirmatory status and robustness of the findings.

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

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: diplopia (1.6%), cerebrovascular accident (1.6%), laryngeal oedema (1.6%), syncope (1.6%), transient ischaemic attack (1.6%).

The registry reports serious adverse events for 2 participants in the valsartan group and 2 in the amlodipine group. The figures at risk for this summary are 63 for valsartan and 62 for amlodipine. Other adverse events are reported for 35 participants in the valsartan group and 51 in the amlodipine group, with the corresponding figures at risk being 63 and 62. These are the posted affected-participant counts; they should not be added together or treated as a direct comparison of event rates without further information about definitions, follow-up, and event handling.

The registry lists diplopia, cerebrovascular accident, laryngeal oedema, syncope, and transient ischaemic attack among the serious-event terms, each at 1.6%. The record does not give further detail about the timing, duration, recurrence, or treatment attribution for these terms in the information. Death counts are not reported in the registry record.

Adverse-event summaries describe what was reported during the study; they do not by themselves determine whether an event was caused by a treatment. Differences in counts are descriptive and should not be interpreted as proof of a safety difference. The registry record does not provide a statistical comparison of these safety summaries.

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

The primary result is an estimate of average change in carotid-femoral PWV over the stated follow-up, comparing valsartan with amlodipine. Both groups had negative estimated changes, and the estimated between-group difference was 0.2 m/s. Its confidence interval includes zero and extends in both directions; the unadjusted p-value was 0.632. Taken together, the posted results do not establish a clear difference in mean change between the groups on this measure.

This is not evidence that the groups are exactly alike. A lack of a statistically clear difference is not the same as an equivalence finding, and the confidence interval leaves uncertainty about the direction and size of the true difference. The registry does not report a clinically important difference threshold, so the results cannot be classified as clinically meaningful or unimportant on that basis.

The endpoint is a vascular measurement, not a direct clinical event outcome. The posted comparison does not establish effects on cardiovascular events, survival, symptoms, or quality of life. The record also does not report outcome data from other populations or follow-up beyond the trial’s stated timeframe. Conclusions should stay within the population, treatments, measurement, and follow-up represented in the registry.

The secondary measures can provide additional descriptive context, but they concern other vascular properties and include multiple comparisons. Their unadjusted results should not be treated as independent confirmation of the primary finding. The record’s incomplete reporting of the analysis plan, missing-data handling, and secondary results also limits the strength of broader claims. In short, the result is an uncertain comparison of average changes in a surrogate measure, not a general verdict about either treatment.

17. Why This Trial Matters Statistically

This trial illustrates a common statistical distinction: a point estimate and its uncertainty answer different questions. The primary difference is close to zero, but the interval is broad enough to include differences in either direction. Focusing only on the point estimate could make the comparison appear more decisive than it is; focusing only on whether a p-value crosses a threshold would also lose information about the range of compatible effects.

The use of least-squares means and standard errors also matters for interpretation. Standard errors quantify uncertainty in estimated means and do not describe how varied individual responses were. The estimated contrast is a summary of group averages, not an account of each participant’s experience. Without the full model specification, readers cannot determine which adjustments were used or reproduce the original analysis from participant-level data.

The study also shows why outcome multiplicity and missingness are part of interpreting results, not administrative details. Several vascular outcomes and follow-up points are listed, yet multiplicity handling and the detailed missing-data approach are not reported in the registry record. Those omissions make it harder to distinguish confirmatory findings from exploratory patterns and to assess the robustness of estimates.

Finally, sample-size illustrations based on an observed effect should not be confused with the trial’s original design or with evidence about the probability that a finding is true. Planning requirements can change sharply depending on the effect a future study aims to detect. Clear reporting of design assumptions, analysis methods, and uncertainty helps readers judge what a trial can support without overstating the scope of its conclusions.

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.

The registry record leaves important details about treatment implementation unclear. Hydrochlorothiazide is listed as an intervention and the brief summary describes its possible addition, but the arm descriptions do not explain when or how it was used. The record therefore does not allow a detailed interpretation of treatment exposure or changes in regimen.

The primary analysis is reported using least-squares means, but the model specification and adjustment variables are not reported in the registry record. The analysis population definition requires baseline and at least one post-baseline measurement, not necessarily the Week 38 measure. The record does not describe missing-data handling, sensitivity analyses, or how incomplete endpoint measurements were included. These gaps limit assessment of the estimate’s robustness.

The secondary outcome list is broader than the secondary results described in the registry record. Results for some named measures are not reported, and the available secondary comparisons are unadjusted. The record does not describe a multiplicity plan or testing hierarchy. It also does not state a threshold for clinically meaningful change in PWV, so statistical estimates cannot be mapped to a registry-defined clinical benchmark.

The primary outcome is a continuous vascular measure, rather than a clinical event. The posted result therefore cannot directly answer questions about event outcomes or longer-term consequences. Safety information is also summarized as affected-participant counts and event terms, without the detail needed to determine attribution or compare event rates rigorously. These limitations are specific to what the registry record reports and do not establish that the unreported procedures were absent from the conduct of the trial.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Efficacy and Safety of Valsartan Versus Amlodipine in Postmenopausal Women With Hypertension — NCT00171054.
• Registry record last updated 2011-06-06; status last verified 2011-06.
• Results first posted 2011-05-03.
• 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 describes a completed Phase 4 randomized, double-blind, parallel-group, active-controlled study in postmenopausal women with mild to moderate hypertension. It compared valsartan 320 mg with amlodipine 10 mg, with possible hydrochlorothiazide addition described in the brief summary. Enrollment was 125.

The primary endpoint was change from baseline to Week 38 in carotid-femoral PWV. Estimated changes were -1.9 m/s for valsartan and -1.7 m/s for amlodipine; the estimated difference was 0.2 m/s, with an unadjusted p-value of 0.632 and a confidence interval spanning zero. The result does not establish a clear difference between groups on this measure. Secondary vascular outcomes and safety summaries provide additional context, but incomplete analysis details, unadjusted secondary comparisons, and unreported missing-data methods limit broader interpretation.