Efficacy, Safety and Tolerability of Multiple Doses of Valsartan in Children With Hypertension With or Without CKD: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Efficacy, Safety and Tolerability of Multiple Doses of Valsartan in Children With Hypertension With or Without CKD (NCT01617681), a randomized phase 3 study. The primary outcome is Change From Baseline in Mean Systolic Blood Pressure (MSBP) at Week 6 Endpoint.

2. Clinical Question

3. Trial Design

This was a phase 3, randomized, parallel-group trial. The registry record describes the first period as a six-week, multicenter, double-blind, double-dummy study intended to evaluate the dose response of valsartan. It lists triple masking, but does not identify which specific groups of people were masked. The randomized groups received valsartan 0.25 mg/kg or 4 mg/kg once daily, with matching placebo solution to support the double-dummy design.

The study included children with hypertension, both with and without CKD. The posted primary results separate the arms by CKD status, so the dose patterns can be considered within those two patient groups. The registry record reports enrollment of 127 participants. The primary analysis population was described as the full analysis set: all randomized patients except one whose guardian did not sign informed consent.

After the randomized period, the trial included a 20-week open-label titration phase. The registry describes valsartan starting at 1 mg/kg, with optional titration to 2 mg/kg and further optional increases in 1 mg/kg increments every 4 weeks, up to a maximum dose of 4 mg/kg. This open-label period is distinct from the blinded randomized dose comparison and should not be read as another randomized contrast.

The registry record lists the study as completed and gives its start and primary completion dates as 2012-11-08 and 2017-01-24. Details of the original sample-size justification, allocation concealment, and the specific roles masked are not reported in the registry record. The formal analysis plan beyond the methods stated for posted outcomes is also not reported in the registry record.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Before assignment: Parallel= Period 1 (Double Blind phase) Single= Period 2 (Open Label phase)

Period 1 Double Blind

Reasons for not completing this period:

Period 2 Open Label

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Full analysis set (FAS) included all randomized patient except for 1 patient that guardian did not sign informed consent

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 in Mean Systolic Blood Pressure (MSBP) at Week 6 Endpoint, measured over Baseline, week 6.

The primary endpoint is change from baseline in mean systolic blood pressure at the week 6 endpoint, measured in mmHg. It is a continuous outcome: each participant’s blood pressure contributes a numerical measurement rather than only an indicator of whether a threshold was reached. A negative change represents a lower measured MSBP at week 6 than at baseline.

The registry describes measuring systolic and diastolic blood pressure three times at intervals of 2–3 minutes, with the arithmetic mean of the readings used as the mean office blood pressure at baseline and week 6. It also says measurements were to be taken in the same position at each visit. Averaging repeated readings is a way to represent blood pressure at a visit while reducing the influence of variation among individual readings.

MSBP is used as the primary measure because the study’s stated question concerns reduction in blood pressure after the randomized dose period. A continuous change measure retains information about the amount and direction of change, rather than reducing the outcome to whether a participant crossed a cutoff. The endpoint does not, by itself, describe longer-term blood pressure, clinical events, or outcomes beyond the period specified. Details about how missing week 6 measurements were handled are not reported in the registry record.

7. Results Posted in the Registry

• CKD Patients Valsartan 4 mg/kg: mean -9.20 versus -1.20 on control; difference -8.00 (95% CI -13.68 to -2.32), standardized effect d = -0.70; z-test p = 0.006.
• Non-CKD Patients Valsartan 0.25 mg/kg: mean -6.90 versus -1.20 on control; difference -5.70 (95% CI -10.61 to -0.79), standardized effect d = -0.57; z-test p = 0.023.
• Non-CKD Patients Valsartan 4 mg/kg: mean -7.80 versus -1.20 on control; difference -6.60 (95% CI -11.56 to -1.64), standardized effect d = -0.66; z-test p = 0.009.

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 Mean Diastolic Blood Pressure (MDBP) at Week 6

• 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:
  • CKD Patients Valsartan 4 mg/kg: mean -6.50 versus 1.30 on control; difference -7.80 (95% CI -12.76 to -2.84), standardized effect d = -0.78; z-test p = 0.002.
  • Non-CKD Patients Valsartan 0.25 mg/kg: mean -1.90 versus 1.30 on control; difference -3.20 (95% CI -7.49 to 1.09), standardized effect d = -0.37; z-test p = 0.144.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for CKD Patients Valsartan 4 mg/kg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Non-CKD Patients Valsartan 0.25 mg/kg and the control. The interval gives the range of effects that remain compatible with the data.

Patients Achieving <90th Percentile for Age, Gender and Height at Week 6 Endpoint in Both MSBP and MDBP

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • CKD Patients Valsartan 4 mg/kg: 29.0% (9/31) versus 19.4% (6/31) on control; risk difference 9.7 percentage points (95% CI -11.5 to 30.9), risk ratio 1.50 (0.61–3.71); unadjusted two-proportion z-test p = 0.374.
  • Non-CKD Patients Valsartan 0.25 mg/kg: 21.2% (7/33) versus 19.4% (6/31) on control; risk difference 1.9 percentage points (95% CI -17.8 to 21.6), risk ratio 1.10 (0.41–2.90); unadjusted two-proportion z-test p = 0.854.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between CKD Patients Valsartan 4 mg/kg and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Non-CKD Patients Valsartan 0.25 mg/kg and the control. The interval gives the range of effects that remain compatible with the data.

CKD Patients Achieving Urine Albumin Creatinine Ratio Percentage Reduction (UACR) >=25% at Week 6

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • CKD Patients Valsartan 4 mg/kg: 33.3% (9/27) versus 44.4% (12/27) on control; risk difference -11.1 percentage points (95% CI -36.9 to 14.7), risk ratio 0.75 (0.38–1.48); unadjusted two-proportion z-test p = 0.402.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between CKD Patients Valsartan 4 mg/kg and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes provide additional views of blood-pressure change and threshold attainment, as well as a kidney-related measure among CKD participants. Taken together, their pattern is mixed rather than uniformly aligned across populations and outcome types. The sponsor reports some dose contrasts for continuous blood-pressure measures, while the reported binary comparisons are less decisive, with uncertainty that includes no difference.

These findings are related to, but do not substitute for, the primary systolic endpoint. A secondary blood-pressure measure can support context about the broader pressure pattern, while threshold-based outcomes answer a different question: whether participants reached specified categories. The UACR outcome concerns a distinct measure among CKD participants. A secondary result that differs in direction or statistical clarity from the primary result is not automatically a contradiction, because the outcomes measure different features and have different precision.

Secondary results carry less weight when many outcomes or comparisons are considered without a reported multiplicity strategy. Repeated testing increases the chance of finding an apparently notable result by chance. The registry record does not report whether multiplicity was controlled, so the secondary analyses should be interpreted as supportive and exploratory rather than treated as independent confirmatory evidence. The record also does not report a formal interaction analysis to establish that effects vary by CKD status.

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

• Change From Baseline in Mean Diastolic Blood Pressure (MDBP) at Week 6
• Patients Achieving <90th Percentile for Age, Gender and Height at Week 6 Endpoint in Both MSBP and MDBP
• CKD Patients Achieving Urine Albumin Creatinine Ratio Percentage Reduction (UACR) >=25% at Week 6

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous, and the registry reports least-squares means with standard errors for the randomized arms. A mean summarizes the central value of a set of measurements. A standard error describes the statistical uncertainty around an estimated mean; it is not the same as the spread of individual participants’ blood-pressure measurements. Because the posted arm values are adjusted least-squares means, they should not automatically be treated as raw averages.

The sponsor reports ANCOVA analyses for dose comparisons. In general, analysis of covariance (ANCOVA) compares outcome values between groups while accounting for one or more covariates. It can improve precision when relevant baseline information is included, but the covariates and detailed model specification are not reported in the registry record. The sponsor’s estimates and confidence intervals therefore describe the posted ANCOVA results, while the registry record does not provide enough detail to reproduce the model fully.

The recalculated continuous comparisons use the posted arm means and standard errors to make simple unadjusted comparisons. These recalculations are not the same as the sponsor’s adjusted ANCOVA results. Their standard deviations are described as approximate, and they rely on summary information rather than participant-level data. They are useful as a transparent supplementary calculation, but they cannot account for the sponsor’s adjustment or verify the analysis dataset and model. Because the registry record indicates a discrepancy, the sponsor’s own analysis takes precedence.

A confidence interval gives a range of values compatible with the observed data under the analysis assumptions. For a difference in means, zero represents no difference between groups. If an interval includes zero, the data do not rule out no difference at the stated confidence level; if it excludes zero, the estimate is less compatible with no difference under that model. This does not make an interval a probability statement about the true value, nor does it show that every value in the interval is equally plausible. The interval’s width communicates precision: narrower intervals indicate more precise estimates than wider ones.

The registry also reports binary secondary outcomes as participant counts and sponsor analyses using odds ratios. A binary outcome distinguishes whether a specified event or threshold was met. An odds ratio compares the odds of that outcome between groups; a value of one corresponds to equal odds under the comparison. The recalculations for binary endpoints use risk differences, which compare proportions on an absolute scale. These are different effect measures and should not be read as interchangeable. For example, an odds ratio and a risk difference can communicate the same underlying comparison in distinct ways and can have different numerical scales.

The trial separates CKD and non-CKD groups in its posted endpoint results. Such subgroup results can help describe patterns, but separate estimates do not alone establish that subgroup effects truly differ. Comparing whether one subgroup result is statistically distinguishable from zero and another is not is not a test of the difference between subgroup effects. The registry does not report a formal interaction test, so a claim that CKD status modifies the dose contrast is not supported by the posted analyses.

Multiple outcomes and comparisons also affect interpretation. When many hypotheses are examined, some apparently notable results can occur by chance even if there are no corresponding underlying effects. Adjusting for multiple comparisons is one approach to controlling that concern, while prespecifying a small number of primary questions is another. The registry record identifies a primary outcome and several secondary outcomes, but does not report a multiplicity adjustment or enough detail to establish how the full family of analyses was handled. The posted secondary p-values should therefore be treated as unadjusted unless the sponsor’s analysis description says otherwise.

For the binary outcomes, sparse counts can produce imprecise estimates. In general, fewer observed events provide less information about the underlying event probability and can make confidence intervals wide. For continuous measures, variability among participants also matters: greater variability makes a mean contrast less precise when other features are similar. These are general statistical principles; the registry record does not report individual-level distributions that would allow a fuller assessment of these features.

The sample-size planning illustrations use the observed effect as a starting point and consider smaller fractions of that effect. They are not the original trial’s design calculations. The stated assumptions are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. The trial’s own sample-size justification and original planning assumptions are not reported in the registry record. The illustrations estimate the participants per arm needed under their assumptions, rather than describing the number actually enrolled in each group or the probability that this completed trial had a positive result.

11. Confidence Intervals and Precision

The primary systolic blood-pressure estimates have different precision across the reported dose comparisons. For the CKD subgroup, the sponsor’s ANCOVA estimate is -7.9 mmHg, with a 95% confidence interval from -13.86 to -2.01. This interval lies below zero but spans a range of possible contrast sizes. It supports a direction of difference under the sponsor’s model more clearly than it fixes the exact magnitude.

For participants without CKD, the sponsor’s estimate is -0.9 mmHg, with a 95% confidence interval from -5.07 to 3.20. Because this interval includes zero and extends in both directions, it is not precise enough to determine the direction of the dose contrast. The estimate near zero should not be mistaken for proof of equivalence; equivalence would require a prespecified margin and an analysis designed to assess it, neither of which is reported in the registry record.

Confidence intervals express uncertainty about estimated group contrasts under the analysis model. They are not ranges containing every participant’s response, and they do not account for every possible source of uncertainty, such as unreported modeling choices or missing-data assumptions. The sponsor’s ANCOVA intervals and the unadjusted recalculated intervals also arise from different methods, so their differences should not be attributed solely to random variation.

For binary secondary outcomes, the reported estimates are also uncertain, with intervals that allow more than one interpretation. Limited event counts can contribute to this imprecision. Overall, the precision is sufficient to describe some estimated contrasts, but it is more limited for determining their exact size, particularly where intervals include the null value. The registry record does not report a clinically important difference threshold that would allow the intervals to be judged against such a benchmark.

12. Planning a Similar Trial: Sample Size

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

The sample-size illustrations express requirements as participants per arm for the continuous and binary outcomes described. They are not total trial enrollment figures and do not represent observed participant counts. The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. The calculations use the observed effect as a reference and also consider planning for 75% and 50% of the observed effect.

The 80% power column gives the number of participants per arm estimated to provide an 80% chance of detecting the effect being planned for, if that effect and the other assumptions used in the calculation hold. The 90% power column gives the corresponding number for a 90% chance. These are design-planning concepts, not guarantees about what a future study will find. Smaller effects are harder to distinguish from random variation, so planning to detect a smaller fraction of the observed effect requires more participants.

For binary outcomes, the planning figures depend on the observed event proportions and can become especially large when the estimated difference is small. Such estimates are sensitive to the observed rates and should not be read as universal recruitment targets. The registry record does not report the trial’s own original sample-size justification or assumptions, so these illustrations cannot explain why the completed trial enrolled its particular number of participants. 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 = -8.000; pooled standard deviation σ = 11.414.
2. n = 2 × (1.96 + 0.842)² × 11.414² / -8.000² = 32.0, rounded up to 32 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 <- -8                      # observed difference in means
sigma <- 11.4139169438015                     # 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(1617681)
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 = 32 (80% power), 43 (90% power)
 75% of observed effect: n per arm = 57 (80% power), 77 (90% power)
 50% of observed effect: n per arm = 128 (80% power), 172 (90% power)
power.t.test: 32.9 
Simulated power at n = 32 per arm: 0.793 (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 reported ANCOVA analyses for the primary systolic endpoint, with separate dose comparisons in the CKD and non-CKD groups. In CKD participants, the reported dose contrast was -7.9 mmHg with a 95% confidence interval from -13.86 to -2.01. In participants without CKD, the reported contrast was -0.9 mmHg with a 95% confidence interval from -5.07 to 3.20. The first interval excludes zero; the second includes zero.

The recalculations are simple unadjusted estimates derived from posted arm summaries. They use the CKD 0.25 mg/kg arm as the reference, so some of their contrasts are not the same comparisons as the sponsor’s within-subgroup dose analyses. Even where the comparison aligns, differences can arise because ANCOVA and an unadjusted summary-statistic calculation do not use the same model. The sponsor’s model details are not fully reported, limiting direct replication.

The registry record flags a discrepancy between the sponsor analyses and the recalculations. Accordingly, the sponsor’s own analysis takes precedence for the trial’s reported dose comparisons. The recalculations can serve as a supplementary check on the direction and approximate scale of posted arm values, but should not replace the sponsor’s adjusted result or be presented as an independent confirmation.

15. Multiplicity, Missing Data and Analysis Populations

The registry record identifies one primary endpoint and lists secondary outcomes, but the complete prespecified statistical analysis plan is not reported in the registry record. In particular, it is not reported whether the sponsor adjusted for multiple comparisons across endpoints, dose contrasts, and CKD subgroups. Without that information, secondary p-values should not be treated as if they were protected from the increased chance of false-positive findings that can arise when many hypotheses are tested.

It is also not reported whether there were interim analyses, whether any stopping rules were used, or whether outcome analyses followed a hierarchy that would preserve a particular confirmatory interpretation. These details matter because they affect how nominal significance levels should be understood. Their absence from the registry record does not show that such procedures were or were not used; it means they cannot be assessed from the posted information.

The primary endpoint population is described as the full analysis set, excluding one randomized patient because the guardian did not sign informed consent. However, the registry record does not report how missing baseline or week 6 blood-pressure values were handled, whether all randomized participants with available data were included in each analysis, or whether imputation or other missing-data methods were used. The effects of missing data therefore cannot be evaluated from the posted record.

The registry reports ANCOVA for sponsor analyses but does not provide the full model specification, covariates, or diagnostics. It also does not report a formal test of interaction between dose and CKD status. These gaps limit assessment of subgroup claims and exact reproduction of the sponsor’s estimates. The original sample-size justification and any adjustments to the planned analysis are not reported in the registry record.

16. Safety Results

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

Deaths

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: gastroenteritis (1.7%), gastritis (1.6%), bronchitis (1.6%), aggression (1.6%), oedema peripheral (0.8%).

During the blinded dose period, the registry reports serious adverse events among 2 of 64 participants at 0.25 mg/kg and 2 of 62 participants at 4 mg/kg. In the open-label group, serious adverse events were reported among 6 of 120 participants. The registry reports zero deaths in each of these groups. These counts describe the posted safety record and should be considered in light of the different group definitions and exposure periods.

The record also lists other adverse events among 19 of 64 participants in the lower-dose group, 13 of 62 in the higher-dose group, and 62 of 120 in the open-label group. The open-label experience is not a randomized comparison with the blinded groups. The registry lists serious-event terms including gastroenteritis, gastritis, bronchitis, aggression, peripheral oedema, and mastoiditis, with the corresponding percentages in its safety record.

Event counts alone do not establish whether an event was caused by treatment, and the posted summary does not provide the clinical detail needed to compare event severity, timing, or exposure-adjusted rates. These figures describe reported events; they do not support medical advice or a general safety conclusion beyond the information recorded.

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

The primary results describe changes in measured systolic blood pressure during the randomized six-week period and estimated contrasts between dose groups within CKD subgroups. The sponsor’s analysis reports a contrast whose confidence interval excludes zero for the CKD subgroup, while the reported contrast for participants without CKD has an interval that includes zero. This is a statistical description of the posted outcomes, not a conclusion about whether a treatment should be used.

The estimates do not mean that every participant experienced a change equal to the group mean. They also do not establish the exact size of an effect, especially where confidence intervals are broad. A result that is not statistically distinguishable from zero does not demonstrate that the groups are identical; a result that is distinguishable from zero does not, by itself, establish clinical importance. The registry record does not state a threshold for a clinically meaningful change.

The comparison concerns the specified doses, population, endpoint, and time period. It does not establish effects beyond week 6, nor does the open-label titration period provide a randomized dose comparison. Results should not automatically be generalized to children outside the recorded age range, to populations not described, or to outcomes that were not posted.

Finally, subgroup-specific estimates do not prove that CKD status changes the dose response. Establishing that requires a direct interaction analysis, which is not reported in the registry record. The results are best read as estimates with defined populations and substantial methodological limits, rather than as a universal statement about valsartan or childhood hypertension.

18. Why This Trial Matters Statistically

This trial illustrates why analysis populations and comparisons must be read precisely. The sponsor’s primary analyses compare the two randomized doses within CKD subgroups, while simple recalculations use a particular reference arm from the posted summaries. Those contrasts are not interchangeable. Distinguishing adjusted sponsor analyses from unadjusted recalculations prevents a technically correct calculation from being assigned the wrong scientific meaning.

It also demonstrates how effect estimates and confidence intervals add information beyond a single significance label. The CKD and non-CKD estimates differ in their precision, and the intervals communicate how much uncertainty remains about the magnitude and direction of each contrast. This is more informative than treating a p-value as a binary verdict.

The outcome structure is another useful statistical lesson. Continuous blood-pressure change, reaching a percentile threshold, and change in a urine measure are different endpoints, each with different information and precision. Results across them need not be identical. Secondary comparisons also warrant caution when the multiplicity plan is not reported.

Finally, the discrepancy between sponsor analyses and summary-statistic recalculations makes transparent reporting especially important. The registry record gives enough information to describe the sponsor’s stated contrasts, but not enough to reproduce every model choice or resolve all missing-data and multiplicity questions. That distinction between what can be estimated and what remains unreported is central to careful interpretation.

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 full statistical analysis plan, the ANCOVA covariates, or detailed model diagnostics. This limits independent reproduction of the sponsor’s adjusted estimates. It also does not report the handling of missing outcome data or any imputation methods, so the possible influence of missingness cannot be assessed.

The trial’s original sample-size justification is not reported. The planning illustrations are based on observed effects and specified assumptions, not the original design rationale. The registry record also does not report multiplicity procedures, interim analyses, or a formal dose-by-CKD interaction test. Consequently, secondary findings and subgroup contrasts require caution.

The primary comparison took place over the six-week blinded period. The later titration phase was open-label, so it cannot be interpreted as a randomized comparison of doses. The posted summaries do not provide individual participant data, preventing checks of distributional features, outliers, or alternative model specifications. The discrepancy between the sponsor analysis and unadjusted recalculation further reinforces that the summary-based estimates should not be treated as a replication of the sponsor model.

These limitations are specific to what the registry record reports and leaves unreported. They do not establish that procedures were absent; they restrict what can be verified from the posted record.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Efficacy, Safety and Tolerability of Multiple Doses of Valsartan in Children With Hypertension With or Without CKD — NCT01617681.
• Registry record last updated 2017-09-27; status last verified 2017-08.
• Results first posted 2017-09-27.
• 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

NCT01617681 is a completed phase 3 randomized, parallel-group study of valsartan in children aged 1–5 years with hypertension, with or without CKD. The blinded, double-dummy period compared 0.25 mg/kg with 4 mg/kg once daily over six weeks, followed by an open-label titration period.

The primary endpoint was change from baseline in mean systolic blood pressure at week 6. The sponsor’s ANCOVA analysis reported different degrees of precision across CKD subgroups: the CKD dose contrast interval excluded zero, while the non-CKD interval included zero. The posted secondary outcomes span continuous blood-pressure, threshold-attainment, and UACR measures, with uncertainty and multiplicity considerations affecting interpretation.

Important details—including the original sample-size justification, missing-data methods, multiplicity procedures, and formal subgroup interaction testing—are not reported in the registry record. The sponsor’s analyses take precedence over discrepant unadjusted recalculations.