Comparison of Chronocort® With Standard Glucocorticoid Therapy in Patients With Congenital Adrenal Hyperplasia: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Comparison of Chronocort® With Standard Glucocorticoid Therapy in Patients With Congenital Adrenal Hyperplasia (NCT02716818), a randomized phase 3 study. The primary outcome is Change From Baseline to 24 Weeks of the Mean of the 24-hour Standard Deviation Score (SDS) Profile for 17-OHP.

2. Clinical Question

3. Trial Design

This was a phase 3 randomized, parallel-arm comparison of Chronocort® and standard glucocorticoid replacement therapy in people with congenital adrenal hyperplasia. The registry record lists enrollment as 122 and describes the study as open-label, so participants and treating personnel were not masked to assigned treatment. The study status is completed. Its recorded start date is 2016-02-22, and its primary completion date is 2018-07-28.

The treatment period was 6 months, with the primary outcome assessed at 24 weeks. Chronocort® was posted as oral capsules, with starting dose based on the participant's previous glucocorticoid therapy and subsequent titration to effect. Participants assigned to standard therapy continued their previous oral glucocorticoid therapy, also titrated to effect. The registry describes admissions for four overnight stays to obtain 24-hour endocrine profiles.

Dose-titration decisions in both groups were made by a central independent physician who was blinded to treatment arm and used information generated from the endocrine profiles. The registry says the same titration rules applied in both arms, with the stated aim of providing the same opportunity for treatment optimization and androgen control. This feature concerns the titration decision process; it does not make the overall trial blinded, which the registry classifies as open-label.

The registry record reports the planned enrollment, but the primary efficacy summaries concern an analysis population defined by receipt of treatment, an evaluable Week 24 profile, and absence of major protocol violations. Those analysis-set conditions mean the reported efficacy population is not simply identified by the enrollment figure. Further details about the original design assumptions, including the sample-size justification, are 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: Following written informed consent and screening tests (Visit 0), eligible participants were called back for the baseline visit. As part of the baseline assessment, participants were admitted overnight for a 24- hour endocrine profile whilst remaining on their standard therapy. Participants were then randomised to Chronocort or standard therapy.

Overall Study

Analysis population for the primary outcome, as defined in the registry: The efficacy evaluable analysis set (EES) comprised all participants who were randomised into the study, who received at least one dose of Chronocort or standard GC therapy, and who had an evaluable Week 24 17-OHP 24-hour hormone profile, and who had no major protocol violations. Total sum of participants in the EES = 105.

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 24 Weeks of the Mean of the 24-hour Standard Deviation Score (SDS) Profile for 17-OHP, measured over 24 weeks.

The primary endpoint is change from baseline to 24 weeks in the mean 24-hour standard deviation score profile for 17-OHP, also called 17-hydroxyprogesterone. The score is expressed as a z-score. A z-score describes a measurement relative to a reference distribution in standard deviation units; the registry states that a negative score indicated greater 17-OHP control compared with baseline, defined as 0.

The profile combines repeated measurements across a 24-hour hormone profile. The registry says the mean was calculated from 13 SDS values, with the first and last values each given half the weight of intermediate values. The primary efficacy variable used a natural-log transformation of the mean 24-hour SDS for the natural logarithm of 17-OHP. The detailed description therefore distinguishes the transformed analysis variable from the broader endpoint name used in the outcome listing.

Repeated measures over the day are relevant because the endpoint is intended to represent the hormone profile across 24 hours rather than a single measurement at one time. The score and profile provide a standardized way to express the direction and magnitude of change from baseline. The endpoint is a biochemical measure; by itself, it does not establish effects on symptoms, long-term health, or other outcomes not measured by this endpoint. Further details about the reference range used to calculate SDS values are not reported in the registry record.

7. Results Posted in the Registry

• Chronocort®: mean -0.40 versus -0.17 on control; difference -0.23 (95% CI -0.54 to 0.08), standardized effect d = -0.28; z-test p = 0.146.

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 to 24 Weeks of the Mean of the 24-hour Standard Deviation Score (SDS) Profile for A4

• 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:
  • Chronocort®: mean 0.11 versus -0.04 on control; difference 0.15 (95% CI -0.17 to 0.48), standardized effect d = 0.18; z-test p = 0.353.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Chronocort® and the control. The interval gives the range of effects that remain compatible with the data.

17-OHP and A4 by Individual Baseline Treatment Strata.

• 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:
  • Pre-Baseline - Prednisone/Prednisolone - 17-OHP: mean -0.06 versus -0.25 on control; difference 0.19 (95% CI -0.26 to 0.64), standardized effect d = 0.24; z-test p = 0.415.
  • Pre-Baseline - Chronocort vs. Hydrocortisone - 17-OHP: mean -0.43 versus -0.25 on control; difference -0.18 (95% CI -0.60 to 0.24), standardized effect d = -0.22; z-test p = 0.395.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Pre-Baseline - Prednisone/Prednisolone - 17-OHP 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 Pre-Baseline - Chronocort vs. Hydrocortisone - 17-OHP and the control. The interval gives the range of effects that remain compatible with the data.

Number of Participants With 17-OHP and A4 Levels in the Optimal Range at 9:00 at Week 24 Visit

• 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:
  • Chronocort - 09:00h Response - 17-OHP: 56.6% (30/53) versus 57.7% (30/52) on control; risk difference -1.1 percentage points (95% CI -20.0 to 17.8), risk ratio 0.98 (0.70–1.37); unadjusted two-proportion z-test p = 0.910.
  • Chronocort - 09:00h Response - A4: 47.2% (25/53) versus 57.7% (30/52) on control; risk difference -10.5 percentage points (95% CI -29.5 to 8.5), risk ratio 0.82 (0.57–1.18); unadjusted two-proportion z-test p = 0.280.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Chronocort - 09:00h Response - 17-OHP 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 Chronocort - 09:00h Response - A4 and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary outcomes cover another 24-hour steroid profile measure, subgroup summaries by baseline treatment, and the number of participants in an optimal range at 9:00. The registry also lists body-composition outcomes based on DEXA, including fat mass, lean mass, and bone mineral density. Numerical results for those body-composition outcomes are not reported in the registry record.

Across the posted continuous and binary secondary comparisons, the reported intervals include values consistent with no group difference. The secondary evidence therefore does not provide a clearly distinct pattern that overturns the primary comparison's uncertainty. These outcomes add context about related biochemical measures and a time-specific response, but they are not interchangeable with the primary 24-hour 17-OHP profile.

Secondary outcomes can help characterize a trial, but they generally carry less confirmatory weight when many outcomes or subgroup comparisons are examined. The registry record lists multiple outcome measures and analyses, while a multiplicity-adjustment plan is not reported in the registry record. Without such a plan, unadjusted p-values across multiple comparisons increase the chance that at least one apparently notable result arises by chance. This is a general statistical concern, not a claim that any specific posted finding is false.

Subgroup estimates should also be interpreted with attention to the number of observations in each baseline-treatment category. Some listed categories have small group counts, making their estimates less precise. The subgroup analyses are descriptive context in the absence of reported prespecification, interaction tests, or a multiplicity strategy. The registry record does not report enough information to establish that these comparisons were designed to support separate treatment conclusions.

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

• Change From Baseline to 24 Weeks of the Mean of the 24-hour Standard Deviation Score (SDS) Profile for A4
• 17-OHP and A4 by Individual Baseline Treatment Strata.
• Number of Participants With 17-OHP and A4 Levels in the Optimal Range at 9:00 at Week 24 Visit
• Changes Relative to Standard Glucocorticoid Therapy in Body Composition (DEXA - Fat Mass and Lean Mass)
• Changes Relative to Standard Glucocorticoid Therapy in Body Composition (DEXA - Bone Mineral Density) - Measured at All Sites Except Germany.

9. Statistical Interpretation

10. Statistical Methods Explained

What does the primary ANCOVA estimate?

The registry reports an ANCOVA for the primary comparison, described as a mean difference in final values. In general, analysis of covariance compares groups at follow-up while accounting for a baseline measurement and any other covariates specified in the model. This can yield an adjusted estimate that differs from a simple contrast of group change summaries. The covariates and full model specification are not reported in the registry record, so the exact adjustment cannot be reconstructed from the posted results.

The separate recalculation uses the posted group means and standard deviations to form an unadjusted comparison of the change summaries. It is useful as a transparent summary of the available descriptive statistics, but it is not a replacement for the trial's own analysis. The recalculation does not incorporate individual participant data, baseline adjustment, or other model features that might have been used in the sponsor's analysis.

How should a mean difference be read?

A mean difference expresses the contrast between group averages in the endpoint's measurement scale. Its direction depends on which group is subtracted from which. For this outcome, the registry says a negative z-score indicates greater 17-OHP control relative to baseline, but that definition does not change the need to check the stated comparison direction. A confidence interval around the mean difference represents uncertainty about the estimated contrast under the analysis assumptions; it does not describe the range of individual participant outcomes.

In general, a confidence interval is a range of values compatible with the observed data and statistical model at the stated confidence level. If it includes zero for a difference, the data do not rule out no group difference at that level. The interval also indicates precision: a narrower interval conveys a more tightly estimated contrast, while a wider one leaves more uncertainty. These interpretations depend on the model and its assumptions.

What does the 24-hour profile contribute?

The endpoint is based on repeated hormone measurements through a 24-hour profile rather than one time point. The registry describes 13 log-transformed 17-OHP values and a weighted mean of their SDS values, with the first and last observations weighted one half relative to intermediate observations. Repeated observations can describe variation across the day, but the registry's summary endpoint reduces them to a single profile mean. Details of how incomplete profiles were handled are not reported in the registry record.

In general, analyses of repeated observations can be sensitive to how within-participant correlation, missing measurements, and transformations are handled. The registry gives the endpoint's transformation and weighting description, but the full statistical model and diagnostic checks are not reported in the registry record. It would therefore be inappropriate to infer additional modeling steps or assumptions from the endpoint definition alone.

How do the secondary methods differ?

For the continuous secondary outcome concerning A4, the posted summaries include group means and an unadjusted mean-difference recalculation. The sponsor reports ANCOVA for final values. The outcome describing the number of participants in an optimal range is binary, and the sponsor reports logistic regression with an odds ratio. In general, an odds ratio compares the odds of an outcome between groups; it is not the same measure as a risk difference and can be less intuitive to interpret directly. The registry's complete model specifications are not reported.

Unadjusted calculations and sponsor-reported analyses answer related but not necessarily identical statistical questions. The former are reconstructed from group summaries; the latter are the analyses recorded by the sponsor. Differences can arise from adjustment, analysis populations, or modeling choices. The posted record does not contain enough detail to determine every reason for any difference, so each estimate should be identified by its method rather than treated as interchangeable.

Why do assumptions matter?

Every inferential method relies on assumptions about the data and analysis. For example, a mean-based analysis summarizes a continuous outcome and can be influenced by skewness or unusually variable observations. In general, over-dispersion means that observed variability is greater than a model expects; if relevant, it can affect standard errors and interval coverage. The registry record does not report a finding of over-dispersion for these outcomes, so it should not be assumed to have occurred.

Randomization supports a treatment-group comparison by assigning treatment independently of participant characteristics in expectation. It does not remove uncertainty, guarantee that every baseline characteristic is balanced, or resolve missing-data concerns. The registry identifies randomized allocation, but detailed information about sequence generation, concealment, baseline adjustment variables, missing-data methods, and sensitivity analyses is not reported in the registry record.

11. Confidence Intervals and Precision

The sponsor's primary ANCOVA estimate is -0.069, with a 95% confidence interval from -0.299 to 0.161. Because this interval spans zero, the reported data are compatible with a range of adjusted differences that includes no difference, as well as differences in either direction. The interval conveys uncertainty around the estimated group contrast; it does not mean that 95% of individual participant outcomes fall within those limits.

The unadjusted recalculation of the mean change contrast is -0.231. Its confidence interval also includes zero. The two estimates should be read separately because the recalculation is unadjusted and based on posted summary statistics, whereas the sponsor reports ANCOVA for final values. Their differing magnitudes do not by themselves indicate an error or a contradiction. The full ANCOVA specification and individual participant data are not reported in the registry record, preventing a reconstruction of the adjusted result.

Precision is not the same as statistical significance or clinical importance. A wide interval leaves more possible values consistent with the data; a narrow interval constrains that range more closely. Whether any particular difference would matter clinically requires a prespecified meaningful threshold or other clinical context, which is not reported in the registry record. The interval alone cannot establish equivalence, absence of effect, or a meaningful benefit.

The A4 secondary outcome's reported ANCOVA interval also includes zero, as does the interval for the binary 17-OHP comparison reported as an odds ratio. These intervals describe uncertainty for different outcome scales and should not be directly compared with the primary endpoint interval as if they measured the same quantity. The registry does not report a multiplicity adjustment for these secondary analyses.

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 based on the observed effect, not the trial's original design calculation. For the continuous outcomes, the figures are participants per arm. For time-to-event outcomes, figures would represent total events, but no time-to-event planning row is reported for these outcomes.

The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The detectable effect is set to the stated fraction of the observed effect. The trial's own original design assumptions and sample-size justification are not reported in the registry record, so these planning figures should not be read as a reconstruction of the trial protocol.

The 80% power column means the illustrative number of participants per arm that would give an 80% chance of detecting the specified effect under those assumptions, if the assumptions and effect size held. The 90% power column represents a higher target chance of detecting that effect and therefore generally requires more participants per arm. Smaller target effects require larger participant numbers because they are harder to distinguish from random variation.

For example, the primary outcome planning rows show increasing participant requirements as the assumed detectable effect is reduced from 100% to 75% and then 50% of the observed effect. Those are scenario comparisons, not forecasts of what a future study will achieve. The same planning framework is applied to the posted comparisons, but the effect estimates are uncertain and can be unstable, especially for comparisons with limited data. This is not observed power: it is a planning illustration, not a measure of the probability that the completed trial detected an effect.

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 = -0.231; pooled standard deviation σ = 0.815.
2. n = 2 × (1.96 + 0.842)² × 0.815² / -0.231² = 195.4, rounded up to 196 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 <- -0.231                      # observed difference in means
sigma <- 0.814903117000473                     # 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(2716818)
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 = 196 (80% power), 262 (90% power)
 75% of observed effect: n per arm = 348 (80% power), 465 (90% power)
 50% of observed effect: n per arm = 782 (80% power), 1,047 (90% power)
power.t.test: 196.3 
Simulated power at n = 196 per arm: 0.800 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The sponsor's reported primary analysis is an ANCOVA comparison of final values. It estimates a mean difference of -0.069, with a 95% confidence interval from -0.299 to 0.161 and a reported p-value of =0.552. The interval includes zero. The unadjusted recalculation from the posted change summaries gives a mean difference of -0.231 and an unadjusted p-value of 0.146; its interval also includes zero.

These results should not be treated as duplicate calculations of exactly the same estimand. ANCOVA may account for baseline values and model covariates, while the recalculation uses aggregate means and standard deviations without adjustment. The registry record does not provide the full sponsor model specification or individual-level data needed to reproduce the ANCOVA. Thus, the sponsor analysis is the primary inferential result recorded for the trial, and the recalculation is supplementary context rather than a substitute.

The two analyses agree in the limited sense that neither reported interval excludes zero. They differ in estimated magnitude, which is unsurprising when methods and target quantities differ. The registry does not identify a discrepancy between the recalculation and reported analysis. No conclusion about why the estimates differ beyond their stated methods is warranted from the registry record alone.

15. Multiplicity, Missing Data and Analysis Populations

The registry record lists a primary outcome, several secondary outcomes, and multiple analyses. It does not report a multiplicity-adjustment procedure or a hierarchy specifying how the secondary hypotheses were to be tested. When many outcomes or comparisons are examined, the chance of at least one apparently positive result can increase if each is judged using an unadjusted threshold. This makes isolated secondary p-values less persuasive than a result from a prespecified primary analysis.

The record reports a primary efficacy analysis set requiring randomization, at least one dose of study treatment, an evaluable Week 24 17-OHP 24-hour profile, and no major protocol violations. This is a restricted analysis population rather than an explicit description of every randomized participant. The registry's description ends with an incomplete statement about the total sum of participants, so further details of the population definition are not reported in the registry record.

The registry record does not report how missing endpoint values were handled, whether participants with incomplete 24-hour profiles were excluded or imputed, or whether sensitivity analyses assessed the effect of missing data. It also does not report the number of participants excluded from the primary efficacy set or the reasons for those exclusions. These omissions limit assessment of whether the analysis population could differ systematically from the randomized population.

In general, excluding participants with unavailable outcome data can affect a treatment comparison if missingness is related to treatment or outcome. Randomization does not automatically resolve this issue after exclusions. The available registry record does not establish that such bias occurred; it simply does not provide enough information to assess the possibility fully.

Details about protocol deviations, analysis-set handling for each secondary outcome, prespecified covariates, and planned interim analyses are not reported in the registry record. No assumptions about these features should be inferred from the posted estimates. The open-label design and the use of a physician blinded to assigned treatment for titration decisions are distinct aspects of the trial: the latter may reduce treatment knowledge in the titration process, but does not establish blinding of outcome assessment or analysis.

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 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: adrenocortical insufficiency (acute) (4.9%), gastroenteritis (3.3%), gastroenteritis viral (1.6%), appendicitis (1.6%), salpingitis (1.6%).

The registry reports serious adverse events for the safety groups, with 61 participants at risk in each arm. Serious adverse events affected 7 participants in the Chronocort® group and 5 in the standard glucocorticoid therapy group. Other adverse events affected 59 participants and 48 participants, respectively. The record reports 0 deaths in each group.

These figures are counts of participants with events, not a comparison adjusted for exposure time, event severity beyond the serious classification, or differences in follow-up. They do not establish that one treatment is safer. The registry lists acute adrenocortical insufficiency at 4.9% among the leading serious-event terms, followed by gastroenteritis at 3.3%; gastroenteritis viral, appendicitis, salpingitis, and tonsilitis are each listed at 1.6%. The registry record does not provide enough detail to infer causality or compare risks for individual event types.

Safety counts should be interpreted alongside the trial's duration and population. The treatment period was 6 months, and the posted counts do not answer questions about longer-term safety or rare events. Further information about event timing, duration, severity grading, and treatment relatedness is not reported in the registry record.

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

The primary result describes the relative change in a biochemical measure over 24 weeks for participants in the reported efficacy analysis. The group summaries are negative, and the registry defines a negative z-score as indicating greater 17-OHP control compared with baseline. The between-group estimates, however, are uncertain: the sponsor's adjusted confidence interval and the unadjusted recalculation's interval both include zero.

This means the posted results do not establish a clear difference between Chronocort® and standard glucocorticoid therapy on the primary endpoint. It does not mean the treatments are proven equivalent, that they have identical effects, or that neither treatment changes the measured outcome. Such conclusions require designs and analysis criteria suited to equivalence or non-inferiority, and those criteria are not reported in the registry record.

The endpoint measures a hormone profile, not every dimension of congenital adrenal hyperplasia or treatment experience. It cannot by itself establish effects on symptoms, daily functioning, long-term complications, quality of life, or outcomes beyond the measured follow-up. Although the registry lists safety and body-composition outcomes, numerical results for the listed body-composition outcomes are not reported in the registry record.

Interpretation is also limited by the open-label design, the restricted primary efficacy analysis population, and the absence of detailed reporting on missing-data methods and multiplicity. The central titration physician was blinded to treatment assignment, but the overall trial was not masked. These features are relevant context for assessing how the results were generated; they do not demonstrate that the findings are biased.

The most defensible reading is therefore specific: the trial reported no clearly separated primary treatment effect in the recorded ANCOVA analysis, and the available summaries leave uncertainty about the size and direction of the difference. Decisions about the clinical importance of any possible difference require context and evidence beyond this statistical comparison.

18. Why This Trial Matters Statistically

This trial illustrates why the analysis method and the estimand matter when interpreting a treatment comparison. A simple difference between posted change summaries is not necessarily the same quantity as an ANCOVA contrast of final values. Presenting both can help readers distinguish a transparent unadjusted recalculation from the sponsor's prespecified or reported inferential approach, while avoiding the mistake of treating them as interchangeable.

The primary outcome also shows how a complex repeated-measure endpoint can be reduced to a single summary. The 24-hour profile uses repeated 17-OHP observations and a stated weighting scheme, while the clinical comparison is expressed as a mean change in a standardized score. That summary supports a group-level comparison but cannot convey every feature of the daily hormone pattern or individual responses.

Precision is central to the interpretation. The primary confidence interval includes no difference and also permits effects in either direction. A non-significant result is not proof of equivalence, and a point estimate alone is not sufficient to judge the range of effects compatible with the data. The posted planning illustrations further demonstrate how strongly sample-size requirements depend on the assumed effect size; they are not the trial's original design calculation.

Finally, the registry provides a useful distinction between randomization, open-label treatment, and blinded dose-titration decisions. These design features address different concerns. The analysis population, missing-data handling, multiplicity strategy, and full statistical model also matter, but several of those details are not reported in the registry record. Clear separation of what is reported from what remains unknown is essential to a calibrated statistical 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 primary efficacy population excludes participants who did not meet the listed treatment, evaluable-profile, and protocol-violation criteria. The registry description is incomplete and does not report the number or characteristics of participants excluded from that set. Missing-data handling and sensitivity analyses are not reported in the registry record, limiting assessment of how unavailable profiles may have affected the result.

The study was open-label, although the central independent physician making dose-titration decisions was blinded to treatment arm. The registry does not report whether outcome assessment or other study processes were blinded. Treatment titration based on endocrine profiles also means the comparison reflects the study's titration procedures, not simply fixed doses.

The posted primary endpoint is a transformed and weighted summary of repeated hormone measurements. The detailed statistical model, covariates, reference distribution for SDS calculation, and handling of incomplete profiles are not reported in the registry record. The sponsor's ANCOVA cannot be independently reconstructed from the aggregate summaries. The recalculated unadjusted contrast therefore provides context but does not replace the sponsor's analysis.

Several secondary outcomes and subgroup comparisons are listed, but a multiplicity plan is not reported. Some baseline-treatment subgroups have small counts, so their estimates may be imprecise. Numerical results for the listed body-composition outcomes are not reported in the registry record. The trial's treatment period was 6 months, and the registry record does not establish longer-term effects. These limitations constrain the scope and certainty of conclusions; they do not by themselves show that the reported analyses are invalid.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Comparison of Chronocort® With Standard Glucocorticoid Therapy in Patients With Congenital Adrenal Hyperplasia — NCT02716818.
• Registry record last updated 2026-10-02; status last verified 2026-09.
• Results first posted 2019-09-04.
• 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

NCT02716818 is a completed, randomized, open-label phase 3 parallel-group study comparing Chronocort® with standard glucocorticoid therapy in congenital adrenal hyperplasia. The registry lists enrollment of 122 and a treatment period of 6 months. The primary outcome was change from baseline to 24 weeks in the mean 24-hour 17-OHP SDS profile.

The sponsor reported an ANCOVA mean difference of -0.069, with a 95% confidence interval from -0.299 to 0.161. The interval includes zero. An unadjusted recalculation from the posted change summaries also has an interval including zero, but it is not the same analysis as the sponsor's ANCOVA. Secondary findings are likewise uncertain, and the registry does not report a multiplicity plan or detailed missing-data methods.