Safety and Efficacy of Valsartan vs Atenolol and Hydrochlorothiazide Combination on Blood Flow in Hypertensive Patients: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Safety and Efficacy of Valsartan vs Atenolol and Hydrochlorothiazide Combination on Blood Flow in Hypertensive Patients (NCT00396656), a randomized phase 3 study. The primary outcome is Difference in Mean Post-treatment Microcirculation at Acetylcholine (ACH) Injected Sites Compared to NaCl Injected Sites.

2. Clinical Question

3. Trial Design

This was a Phase 3, randomized, open-label, multicenter crossover trial, with 30 participants enrolled. The registry lists hypertension as the condition and describes the objective as comparing valsartan with atenolol plus hydrochlorothiazide (HCTZ) for effects on small vessel blood flow. Because the design was crossover, participants received both regimens in sequence rather than remaining in a single treatment group throughout.

The record describes a 2-week washout period before treatment. One sequence received valsartan and then atenolol plus HCTZ; the other received atenolol plus HCTZ and then valsartan. Valsartan was administered for 20 weeks, with a dose of 160 mg for 4 weeks followed by 320 mg for 16 weeks, then tapered to 80 mg for one week. The other regimen included atenolol 100 mg for 20 weeks; the record says atenolol was tapered and HCTZ discontinued after that period. Some arm-description text is incomplete in the registry record, so other regimen details are not reported in the registry record.

The primary outcome was measured at the end of each treatment period, identified as Week 21 and Week 43. The record reports 27 participants for each treatment in the primary outcome results, and defines the primary outcome population as randomized patients with at least one valid post-baseline measurement in both treatment periods. The registry reports no analyses under its reported-analysis entries, so the inferential approach used by the trial investigators, including any crossover-specific modeling, is not reported in the registry record. The record also does not report treatment-sequence results or an assessment of period or carryover effects.

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.

First Treatment Period

Reasons for not completing this period:

Second Treatment Period

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Intent-to-treat (ITT) population: All randomized patients with at least one valid post-baseline primary efficacy measurement in both treatment periods.

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 Difference in Mean Post-treatment Microcirculation at Acetylcholine (ACH) Injected Sites Compared to NaCl Injected Sites, measured over At end of each treatment period (Week 21 and Week 43).

The primary endpoint was the difference in mean post-treatment microcirculation at acetylcholine (ACH)-injected sites compared with NaCl-injected sites. It was measured at the end of each treatment period and expressed in perfusion units. The registry describes these units as an arbitrary measure specific to each laser Doppler scanner, so they are not a universal physical scale that can be directly compared across scanners.

For measurement, 10 µl of ACH at concentrations of 10-7, 10-8, and 10-9 M was injected intradermally at 3 forearm sites; NaCl was injected at 2 forearm sites. Laser Doppler velocimetry measured microcirculation before injection and 12 times during the 30 minutes following injection. The mean difference between the post-injection measurements and the pre-injection measurement was calculated for each site type, and the ACH-site mean was compared with the NaCl-site mean.

Using NaCl-injected sites as a reference helps distinguish the response at sites receiving ACH from the measurement at sites receiving the reference injection. This endpoint was used because the trial sought to assess small vessel blood flow under a local challenge. The result is a measurement of this experimental response, not a direct measure of every aspect of blood flow or vascular function.

7. Results Posted in the Registry

• Atenolol + Hydrochlorothiazide: mean 61.04 versus 61.21 on control; difference -0.17 (95% CI -23.63 to 23.29), standardized effect d = -0.00; z-test p = 0.989.

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.

Difference in Mean Post-treatment Microcirculation at Acetylcholine (ACH) Plus L-NMMA Injected Sites Compared to NaCl Injected Sites

• 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:
  • Atenolol + Hydrochlorothiazide: mean -5.60 versus -9.11 on control; difference 3.51 (95% CI -13.90 to 20.92), standardized effect d = 0.11; z-test p = 0.693.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Atenolol + Hydrochlorothiazide and the control. The interval gives the range of effects that remain compatible with the data.

Difference in Mean Post-treatment Microcirculation at a Sodium Nitroprusside Injected Site Compared to NaCl Injected Sites

• 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:
  • Atenolol + Hydrochlorothiazide: mean 128.14 versus 120.65 on control; difference 7.49 (95% CI -29.51 to 44.49), standardized effect d = 0.11; z-test p = 0.692.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Atenolol + Hydrochlorothiazide and the control. The interval gives the range of effects that remain compatible with the data.

Mean Post-treatment Microcirculation at NaCl Injected Sites

• 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:
  • Atenolol + Hydrochlorothiazide: mean 50.96 versus 44.78 on control; difference 6.18 (95% CI -25.08 to 37.44), standardized effect d = 0.11; z-test p = 0.698.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Atenolol + Hydrochlorothiazide and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary outcomes cover additional microcirculation responses and measures of arterial pressure waveforms. These include ACH with L-NMMA compared with NaCl, a sodium nitroprusside response compared with NaCl, mean microcirculation at NaCl sites, augmentation index, and pulse wave velocity. The registry lists five secondary outcomes, but numeric results are posted for only three of them; results for the other two are not reported in the registry record.

Across the three outcomes with numeric results, the treatment contrasts are imprecise and their confidence intervals include zero. The pattern does not provide a clear, consistent separation between the treatment regimens across these different measures. This is broadly in line with the primary result's lack of a clearly distinguished contrast, but secondary outcomes address different physiological measurements and should not be treated as interchangeable confirmations of the primary endpoint.

The secondary outcomes are exploratory in interpretation because the registry does not report a multiplicity adjustment or a prespecified hierarchy for testing them. When multiple outcomes are examined, the chance of observing apparently notable findings can increase, even when there is no underlying difference. Unadjusted results therefore carry less weight than a single prespecified primary comparison, particularly when the analysis plan and multiplicity strategy are not reported.

The reported-analysis entries are empty, and the registry does not describe the inferential methods for the secondary outcomes. The posted summary statistics can describe the observed means and uncertainty, but they do not establish whether the investigators treated these outcomes as confirmatory, how missing measurements were handled, or whether conclusions were adjusted for the number of outcomes considered. Interpretation should focus on the overall pattern and the documented uncertainty rather than isolating any one secondary estimate.

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

• Difference in Mean Post-treatment Microcirculation at Acetylcholine (ACH) Plus L-NMMA Injected Sites Compared to NaCl Injected Sites
• Difference in Mean Post-treatment Microcirculation at a Sodium Nitroprusside Injected Site Compared to NaCl Injected Sites
• Mean Post-treatment Microcirculation at NaCl Injected Sites
• Arterial Pressure Waveform Augmentation Index at the End of Treatment
• Arterial Pressure Waveform Pulse Wave Velocity at the End of Treatment

9. Statistical Interpretation

10. Statistical Methods Explained

What does a mean difference describe?

A mean is a measure of the center of a continuous outcome. Here, the outcome is the mean microcirculation response, in perfusion units, for each treatment period. A mean difference places the two treatment summaries on a common scale by expressing one relative to the other. The posted contrast is -0.17 for atenolol plus HCTZ relative to valsartan; the registry lists the valsartan mean as 61.21 and the combination-treatment mean as 61.04.

The standard deviation describes the spread of individual measurements around a group mean. The registry reports standard deviations of 38.11 for valsartan and 49.16 for atenolol plus HCTZ. These describe variability among measurements, not the uncertainty in the estimated treatment contrast itself. A standard error and a confidence interval address uncertainty in an estimate, and should not be read as descriptions of individual participant values.

How should the confidence interval be read?

A confidence interval gives a range of values that are reasonably compatible with the observed data under the assumptions of the method used. The primary contrast has a 95% confidence interval from -23.63 to 23.29. Since this range includes zero, the posted results do not distinguish the contrast from zero at the conventional two-sided 0.05 level. The wide span also indicates limited precision: substantially negative and positive contrasts remain compatible with the interval.

A confidence interval is not a probability statement that the true value lies in the particular interval. In general, the confidence level describes the long-run performance of the procedure when its assumptions hold. Its practical interpretation depends on the study design and analysis. Because the registry does not describe the inferential model for this crossover trial, the details of the interval's treatment of within-participant correlation and period effects are not reported in the registry record.

What does the p-value add?

The unadjusted p-value for the primary comparison is 0.989. In general, a p-value measures how unusual the observed data, or data more extreme, would be under a specified null hypothesis and the assumptions of the test. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of an effect. The posted p-value is consistent with the confidence interval including zero. It should not be interpreted as evidence of equivalence or as proof that there is no treatment difference.

The term unadjusted matters because the p-value is not described as corrected for testing multiple outcomes or comparisons. The registry record does not report a multiplicity procedure or the trial's complete statistical analysis plan. It also does not list a reported analysis for the outcome, so the test underlying the posted summary is not detailed in the registry record.

Why does the crossover design matter?

In a crossover trial, each participant receives more than one treatment, and their responses under the different periods can be compared. This can account for stable differences between participants, but the analysis needs to reflect repeated measurements from the same people. Period effects, treatment sequence, and possible carryover from an earlier regimen can also matter. The registry describes the treatment sequences and a washout period, but does not report whether the trial analysis modeled these features or assessed carryover. General statistical guidance is that the design and analysis should be interpreted together; the posted group means alone do not reveal how within-person information was used.

The outcome population definition requires a valid post-baseline primary measurement in both periods. This is relevant in a crossover study because a participant without a valid measurement in either period cannot contribute a complete within-person treatment comparison under that definition. The number of participants excluded from the primary outcome population is not explained in the registry record, and reasons for missing or invalid measurements are not reported in the registry record.

What is general about these methods?

In general, interpretation of a continuous-outcome comparison considers the estimated difference, its uncertainty, the outcome's measurement scale, and the design. Here the scale is described as scanner-specific and arbitrary, which makes the absolute value less readily interpretable outside the measurement setup. The comparison is most directly understood as a difference in the reported perfusion-unit summaries under the trial conditions.

The registry lists the outcome parameter as a mean and its dispersion as a standard deviation. It does not report a prespecified clinically important difference, a minimum relevant effect, or the assumptions used in the original trial's sample-size planning. Those omissions limit judgments about whether the confidence interval excludes effects that would matter to the trial's intended question. The posted summaries support description of the observed data and their uncertainty, but do not provide enough methodological detail to reconstruct the trial's full analysis.

11. Confidence Intervals and Precision

The primary mean difference is -0.17 perfusion units, with a 95% confidence interval from -23.63 to 23.29. The interval crosses zero and spans values on both sides of the point estimate. Thus, the estimate is not precise enough to rule out a range of differences favoring either treatment. The point estimate alone should not be treated as a definitive estimate of the true treatment contrast.

The interval is wide relative to the near-zero point estimate. It reflects uncertainty in the contrast, whereas the reported standard deviations describe the dispersion of outcome values: 38.11 for valsartan and 49.16 for atenolol plus HCTZ. The 27 participants reported for each treatment also indicate that the primary summary comes from a limited analysis population. The registry does not explain why the primary outcome population is smaller than total enrollment.

In general, a confidence interval is useful because it shows both the direction and range of estimates compatible with the data under the analysis assumptions. Here, the range includes zero as well as negative and positive contrasts. It therefore cannot be used to claim equivalence, and it does not establish that a difference of practical importance is impossible. No threshold for a clinically important difference is reported in the registry record.

The registry does not describe how the interval accounts for the paired nature of a crossover design, treatment period, or sequence. That missing analysis detail is relevant to assessing the precision calculation. The result supports a cautious conclusion: the observed contrast is close to zero, but its uncertainty is substantial.

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 figures are planning illustrations expressed as participants per arm, not total events. They use the observed effect as a starting point and show planning for 100% of that observed effect, 75% of the observed effect, and 50% of the observed effect. For example, planning for 100% of the observed effect gives 1,050,794 participants per arm for 80% power and 1,406,715 participants per arm for 90% power. These figures are not the original design assumptions for the trial; those assumptions are not reported in the registry record.

The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. The effect to detect is the stated fraction of the observed effect. In plain terms, the 80% power column represents the planned number per arm under which a study would have an 80% chance of detecting the assumed effect at the stated significance level, if the planning assumptions hold. The 90% column represents a higher chance of detecting that assumed effect, and therefore requires more participants per arm in these illustrations.

Smaller effects are harder to distinguish from random variation, so planning for 75% or 50% of the observed effect requires more participants than planning for the full observed effect. Because the primary observed contrast is -0.17 and close to zero, planning calculations based on fractions of it produce very large figures. These are hypothetical planning results, not observed power for the completed trial. They should not be interpreted as evidence about the chance that the completed trial detected a true effect.

The trial itself was a crossover study, while the listed planning assumptions specify equal allocation between two arms and use a normal approximation. The registry does not report the trial's own sample-size justification or whether it used assumptions tailored to the crossover design. The plotted curve should be read as an illustration of how the planning estimates change with the assumed effect, not as an account of the trial's original design process.

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 = -0.170; pooled standard deviation σ = 43.983.
2. n = 2 × (1.96 + 0.842)² × 43.983² / -0.170² = 1,050,793.3, rounded up to 1,050,794 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 <- -0.170000000000002                      # observed difference in means
sigma <- 43.9833928886802                     # 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(396656)
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 = 1,050,794 (80% power), 1,406,715 (90% power)
 75% of observed effect: n per arm = 1,868,077 (80% power), 2,500,825 (90% power)
 50% of observed effect: n per arm = 4,203,174 (80% power), 5,626,857 (90% power)
power.t.test: 1050794 
Simulated power at n = 1,050,794 per arm: 0.798 (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 one primary outcome and five secondary outcomes. Testing several outcomes creates a multiplicity issue: in general, the more comparisons examined, the greater the chance that at least one result may appear unusual by chance. A prespecified testing hierarchy or adjustment can address that concern, but the registry record does not report a multiplicity plan, a hierarchy among the outcomes, or adjusted p-values. The posted primary p-value is explicitly unadjusted, and secondary comparisons should likewise be treated cautiously in the absence of a reported correction.

The record includes an intent-to-treat population definition for the primary outcome: randomized patients with at least one valid post-baseline primary efficacy measurement in both treatment periods. The posted primary summaries include 27 patients for each treatment, while total enrollment was 30. Reasons that some randomized participants do not appear in the primary outcome population are not reported in the registry record. The record does not describe missing-data methods, imputation, or sensitivity analyses for missing or invalid measurements.

That population definition requires data from both treatment periods. In general, missing one period can complicate a crossover comparison because the within-participant treatment contrast may not be available. The registry does not explain whether participants with incomplete data contributed to any other analyses, or whether any alternative analysis populations were used.

The registry has no reported analyses listed for the outcomes. It therefore does not describe the statistical model, handling of within-participant correlation, period or sequence effects, carryover, or adjustment for other factors. The presence of a randomized crossover design does not by itself establish how those features were handled in analysis. These omissions limit assessment of the robustness and reproducibility of the posted comparisons; they do not establish that the trial investigators did or did not perform particular analyses.

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: diverticulitis (3.3%).

The registry reports serious adverse events affecting 0 of 28 participants in the valsartan group and 1 of 30 participants in the atenolol plus HCTZ group. These are counts of participants reported as affected, not estimates of comparative risk adjusted for the crossover design. The registry lists Diverticulitis at 3.3% among the leading serious-event terms, but does not identify its treatment attribution in the posted details. Death counts are not reported in the registry record.

Other adverse events are reported for 16 of 28 participants during valsartan and 12 of 30 during atenolol plus HCTZ. The record does not provide enough detail to compare event types, timing, duration, severity, or whether a participant experienced more than one event. Nor does it describe an analysis accounting for participants receiving both regimens. These descriptive counts should be read as safety reporting for the recorded treatment periods, not as a causal comparison or as a complete characterization of safety.

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

The primary finding is a posted mean contrast of -0.17 perfusion units for atenolol plus HCTZ relative to valsartan, with a 95% confidence interval from -23.63 to 23.29. The point estimate is near zero, while the interval allows for differences in either direction. The unadjusted p-value of 0.989 is not evidence that the treatments are equivalent; it indicates that the posted test does not distinguish the result from zero under its assumptions.

The finding concerns one specific experimental measure: the post-treatment microcirculation response at ACH-injected sites compared with NaCl-injected sites, measured by laser Doppler velocimetry and expressed in scanner-specific perfusion units. It does not, by itself, answer questions about outcomes outside this measurement or establish how the regimens compare on other clinical endpoints. The endpoint's arbitrary, device-specific scale also means its numerical values should be interpreted in the context of this measurement procedure.

The study was randomized and crossover, and participants were scheduled to receive both treatment regimens. However, the registry does not report the full analysis model, how the within-participant design was handled, or analyses of period, sequence, or carryover effects. The primary analysis population was defined by valid measurements in both treatment periods and included 27 participants per treatment; the record does not explain why this was fewer than the 30 enrolled.

Accordingly, the posted data do not support a firm claim that one regimen has a greater or smaller effect on the measured endpoint. They also do not establish no effect, equivalence, or a clinically important difference. The result is best understood as an uncertain estimate from a small reported outcome population, with important analysis details and the trial's original sample-size justification not reported in the registry record.

17. Why This Trial Matters Statistically

This trial is statistically instructive because its primary point estimate is close to zero while its confidence interval is broad. Looking only at the point estimate or p-value would obscure how much uncertainty remains. The interval shows that the data are compatible with contrasts on either side of zero, so the result is not a demonstration of equivalence or proof of no difference.

The crossover design also highlights why trial structure matters when reading summary statistics. The same participants were intended to receive both regimens, but the registry does not describe the model used to account for repeated measurements or the handling of period and sequence. A simple comparison of treatment-period summaries cannot show whether the analysis made full use of the within-participant design. When analysis details are missing, readers should separate what the posted estimate says from what cannot be verified about its calculation.

The endpoint itself is a specialized physiological measure, reported in perfusion units that the registry describes as arbitrary and scanner-specific. This creates an important distinction between statistical and substantive interpretation: a numerical difference can be estimated, but its practical meaning requires a meaningful-effect threshold and context for the measurement. Neither a threshold nor the trial's original sample-size justification is reported in the registry record.

Finally, the planning illustrations show how sample-size requirements can become very large when based on a small observed contrast, and larger still when planning for smaller fractions of that effect. These calculations are hypothetical and depend on stated assumptions; they are not evidence about the completed trial's observed power. Together, the estimate, its uncertainty, the crossover design, and the limits of the registry's analysis detail demonstrate why statistical conclusions should reflect both the results and the information available about how they were produced.

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 several trial-specific uncertainties. Although the study is described as randomized and crossover, the reported-analysis entries are empty. The statistical model, the use of within-participant comparisons, and any handling of treatment period or sequence are not reported in the registry record. A washout period is described, but an assessment of possible carryover is not reported in the registry record.

The primary outcome population required a valid post-baseline measurement in both periods. Results include 27 participants per treatment, compared with 30 enrolled, but the reason for the difference is not reported in the registry record. Missing-data procedures, sensitivity analyses, and the handling of participants without complete measurements are also not reported in the registry record. The record does not report the trial's original sample-size justification, so the adequacy of planned enrollment for the primary comparison cannot be assessed from that justification.

The endpoint is a scanner-specific, arbitrary perfusion-unit measure, and no clinically important difference is reported. Consequently, the clinical meaning of the observed contrast and the range in its confidence interval cannot be judged against a registry-defined threshold. The record also does not report a multiplicity plan despite listing secondary outcomes, and results for two listed secondary measures are not reported in the registry record.

The trial was open-label, as masking was listed as none. The registry does not report procedures to reduce the influence of awareness of treatment on measurement or assessment. These limitations identify uncertainties in the reported record; they do not establish that particular safeguards or analyses were absent from the conduct of the study.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Safety and Efficacy of Valsartan vs Atenolol and Hydrochlorothiazide Combination on Blood Flow in Hypertensive Patients — NCT00396656.
• Registry record last updated 2011-06-06; status last verified 2011-05.
• Results first posted 2011-06-06.
• 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 Phase 3 randomized, open-label, multicenter crossover trial of valsartan versus atenolol plus hydrochlorothiazide in patients with hypertension. Thirty participants were enrolled. The primary question concerned post-treatment microcirculation at ACH-injected sites compared with NaCl-injected sites, measured in scanner-specific perfusion units at the end of each treatment period.

The primary result reports means of 61.21 for valsartan and 61.04 for atenolol plus HCTZ, with a mean difference of -0.17, a 95% confidence interval from -23.63 to 23.29, and an unadjusted p-value of 0.989. The interval is broad and includes zero; it does not establish equivalence or rule out differences in either direction. The record lists secondary microcirculation results but does not report results for every listed secondary outcome.

The registry does not report the full statistical analysis plan, the original sample-size justification, multiplicity handling, or detailed missing-data methods. These omissions limit how completely the posted summaries can be evaluated, particularly given the crossover design.