Evaluation of Rosacea-related Inflammatory Biochemical Markers in Adult Skin When Treated With Oracea® vs Placebo: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Evaluation of Rosacea-related Inflammatory Biochemical Markers in Adult Skin When Treated With Oracea® vs Placebo (NCT01308619), a randomized phase 4 study. The primary outcome is Change From Baseline in Inflammatory Lesion Counts.

2. Clinical Question

3. Trial Design

The registry describes a completed Phase 4, randomized, double-blind, placebo-controlled, parallel-group trial sponsored by Galderma R&D. The study evaluated daily doxycycline 40 mg, formulated as 30 mg immediate-release and 10 mg delayed-release beads, against placebo in adults with papulopustular rosacea. The listed enrollment was 170. The registry dates the start to 2011-04 and primary completion to 2012-08.

Randomization is intended to support a fair comparison by allocating participants to study groups without relying on clinical judgment about which treatment they receive. Double masking means that the study is described as blinded at two roles or levels, but the registry record does not identify exactly who was masked or how masking was maintained. The parallel design means participants were assigned to a group rather than being described as crossing from one study treatment to another.

The primary outcome was mean change from baseline to week 12 in inflammatory lesion counts. Listed secondary outcomes included biochemical markers assessed through tape stripping and/or skin biopsy, Investigator's Global Assessment scores at week 12, and change in Clinician's Erythema Assessment scores. The posted numerical secondary results include the CEA outcome; numerical results for the listed biochemical marker outcomes and IGA are not reported in the registry record.

The registry record does not report the original sample-size justification, the planned analysis population, the detailed allocation procedure, or the protocol's statistical analysis plan. It also does not report whether interim analyses were planned or conducted. These design details should not be inferred from the fact that the study was randomized, masked, and completed.

4. Participant Flow and Accounting

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

Overall Study

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 Inflammatory Lesion Counts, measured over baseline to week 12.

The primary endpoint is change from baseline to week 12 in inflammatory lesion counts, expressed as a mean number of inflammatory lesions. A change score describes how much the measured count shifted between the start of observation and the stated follow-up, rather than describing the follow-up count alone. A negative mean change indicates that the measured count was lower at follow-up than at baseline, on average. The group means were -4.3 for Oracea® and -3.2 for placebo.

This endpoint is used to compare the average change between the randomized groups. The clinically relevant statistical contrast is therefore not just whether either group changed from its own baseline, but how different the changes were between groups. The posted between-group estimate is -1.1 lesions, calculated as Oracea® minus placebo. Its negative direction reflects a numerically more negative mean change in the Oracea® group. The registry record does not give a threshold for interpreting the clinical importance of a difference in lesion counts.

Inflammatory lesion counts are a clinical measure, while the study objective also concerned rosacea-related inflammatory markers in skin. Considering both types of outcome can describe clinical change alongside biological measurements, but a relationship between them would require appropriate results and analysis. That relationship is not reported in the registry record. The endpoint alone therefore does not establish whether any observed clinical change is linked to changes in the biochemical markers.

7. Results Posted in the Registry

• Oracea®: mean -4.30 versus -3.20 on control; difference -1.10 (95% CI -3.58 to 1.38), standardized effect d = -0.13; z-test p = 0.385.

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 Clinician's Erythema Assessment (CEA) Scores

• 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:
  • Oracea®: mean -1.00 versus -0.80 on control; difference -0.20 (95% CI -1.10 to 0.70), standardized effect d = -0.07; z-test p = 0.664.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Oracea® and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists secondary outcomes covering biochemical markers, IGA scores, and CEA scores. The numerical secondary result posted in the record is for change in CEA scores; numerical results for the listed biochemical-marker outcomes and IGA are not reported in the registry record. This limits the extent to which the stated objective of relating clinical effects to inflammatory markers can be assessed from the posted results.

At a broad level, the available CEA comparison does not provide clear statistical evidence of a between-group difference in the unadjusted recalculation. That pattern does not supply a separate confirmation of the primary lesion-count result. It should be considered alongside the primary result as an additional, uncertain comparison, rather than as evidence that independently resolves the primary endpoint's uncertainty.

Secondary results generally carry less evidential weight when the number of comparisons, their prespecified status, and any multiplicity adjustment are unknown. Looking across several outcomes can make apparently notable findings more likely to arise by chance. The registry record does not report a multiplicity strategy, a hierarchy of secondary endpoints, or the full planned analysis. Accordingly, the CEA result is most appropriately treated as descriptive, and absence of posted biochemical-marker or IGA results should not be read as a null finding.

The planned question about correlation between clinical changes and inflammatory markers is also distinct from whether a treatment-group difference exists for either measure. A correlation analysis requires paired measurements and an estimate of their association. Such an analysis is not reported in the registry record. The available secondary information therefore provides limited support for drawing conclusions about how clinical outcomes and skin markers relate.

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

• Change From Baseline in Biochemical Markers of Rosacea From Tape Stripping and/or Skin Biopsy From Baseline to Week 12
• Investigator's Global Assessment (IGA) Scores at Week 12
• Change From Baseline in Clinician's Erythema Assessment (CEA) Scores

9. Statistical Interpretation

10. Statistical Methods Explained

The main comparison concerns a continuous outcome: mean change in lesion counts. For each group, the registry posts a sample size, a mean change, and a standard deviation. The mean summarizes the average observed change, while the standard deviation describes how dispersed participant-level changes were around that average. These answer different questions. A relatively small standard deviation would indicate more similar changes among participants; a larger standard deviation indicates greater variation.

How to read the between-group estimate

The reported contrast is the Oracea® mean change minus the placebo mean change. The estimate is -1.1 lesions. A negative estimate means the Oracea® group had a more negative average change than the placebo group, using this subtraction order. The estimate is expressed in the original outcome units, so it retains a direct interpretation as a difference in mean lesion-count change. It is an estimate from the observed groups, not a guarantee that the same difference would be observed in another study.

The contrast is more informative for comparing randomized groups than looking only at whether each group's mean moved from baseline. Changes within both groups can occur for many reasons, including the course of the condition, study participation, measurement variation, or treatment. The randomized comparison is designed to help distinguish the difference associated with group assignment from changes common to both groups. The registry result still requires uncertainty assessment and does not itself identify the mechanism behind a difference.

What the confidence interval expresses

A confidence interval describes the precision of an estimate under the assumptions of the statistical method. It gives a range of values compatible with the observed data and that method; it is not a range containing a fixed proportion of individual participant outcomes. The unadjusted recalculated interval for the primary mean difference is -3.581 to 1.381 lesions. Its inclusion of zero indicates that the data do not rule out a zero average difference at the corresponding confidence level. The interval also includes values on either side of zero, so the estimate remains uncertain in both direction and magnitude.

The interval and p-value are related ways of expressing uncertainty, but they are not interchangeable with clinical importance. The p-value of 0.385 is the unadjusted recalculated result for testing a null hypothesis of no mean difference under the calculation's assumptions. It is not the probability that the null hypothesis is true, nor is it the probability that the observed estimate arose by chance. A non-small p-value does not prove that the groups are the same. Likewise, the confidence interval crossing zero does not establish equivalence; an equivalence conclusion requires a defined margin and an analysis designed to assess it, neither of which is reported in the registry record.

Why dispersion matters

Continuous-outcome comparisons depend on both the size of the estimated difference and the variation in participant outcomes. When outcomes vary substantially within groups, the mean difference is estimated less precisely for a given amount of information. Here the posted standard deviations are 7.9 and 8.6, while the between-group estimate is -1.1. This context helps explain why the interval is broad relative to the point estimate. Standard deviations describe observed participant-level variability, whereas the confidence interval describes uncertainty in the estimated group contrast.

Some clinical outcomes can be more variable than a simple normal model would anticipate. In general, over-dispersion means that observed variability exceeds what a particular model assumes. If present and not addressed, it can make standard errors too small and confidence intervals too narrow. The registry record does not report a model-based analysis or an assessment of over-dispersion for this endpoint, so no claim can be made about whether it was examined or relevant.

What is and is not reported about analysis

The registry record lists no reported analyses. The numerical between-group estimate, confidence interval, p-value, pooled standard deviation, and effect-size information in the recalculation are simple unadjusted calculations based on posted summary statistics. They should not be mistaken for a fully specified sponsor analysis. The record does not report covariate adjustment, stratification, missing-data methods, a prespecified analysis population, or a statistical model for the primary comparison. It also does not report whether the analysis followed an intention-to-treat principle or another population definition.

Using summary statistics cannot recover all details of an individual-participant analysis. For example, the posted summaries do not show participant-level distributions, reasons for missing measurements, or whether particular observations were excluded. They also do not reveal any prespecified decisions about transformations, outliers, or sensitivity analyses. Such details are not reported in the registry record and should not be presumed.

Interpreting secondary outcomes

Secondary outcomes can broaden the description of a trial, but they do not automatically have the same evidential status as the primary endpoint. A study may assess several outcomes, time points, or comparisons. Testing many questions increases the possibility that some results will appear noteworthy by chance unless the analysis plan addresses multiplicity. The registry record does not report a multiplicity procedure or a hierarchy for interpreting secondary outcomes. The posted CEA comparison is therefore best read as exploratory or descriptive rather than as independent confirmation of the primary result.

The registry's study objective includes possible correlation between clinical effects and inflammatory markers. Correlation is a distinct statistical question from comparing group means: it asks whether participant-level changes in one measure tend to vary with another. The registry record does not provide a correlation estimate or analysis. The posted primary endpoint comparison cannot answer that question by itself.

11. Confidence Intervals and Precision

Precision concerns how narrowly the data locate the estimated difference, not whether a result is clinically important. The primary mean difference is -1.1 lesions, with an unadjusted recalculated confidence interval from -3.581 to 1.381. The interval spans zero and includes estimates in both directions. Thus the point estimate is not precise enough to rule out a range of possible between-group effects under the calculation used.

The confidence interval should be read as a set of values that are reasonably compatible with the data and the method's assumptions. It is not a statement that the true effect has a specified probability of falling inside the observed interval. It also does not show where most individual participants' changes lie; that is the role of outcome distributions and dispersion measures, not a confidence interval for a mean difference.

The posted group sizes were 84.0 for Oracea® and 86.0 for placebo. Group size contributes to precision, but precision also depends on variability and the analysis method. The standard deviations of 7.9 and 8.6 describe considerable variation in change scores relative to the estimated contrast. No sponsor-reported confidence interval or adjusted primary analysis is reported in the registry record, so the interval discussed is an unadjusted recalculation rather than a documented protocol-based inferential result.

A confidence interval that includes zero should not be interpreted as proof that there is no effect. Conversely, an estimate away from zero does not alone demonstrate a reliable or meaningful difference. The interval's breadth is important: the evidence does not pin down the size or direction of the average contrast with high precision. The registry record also gives no threshold for a clinically meaningful difference in inflammatory lesion counts, so statistical uncertainty cannot be translated into a judgment about clinical importance.

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 justification. The registry record does not report the trial's original sample-size assumptions. The illustration assumes a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. It considers effects equal to the stated fraction of the observed effect. The figures are participants per arm, not total events.

For the primary lesion-count comparison, planning for 100% of the observed effect gives 886 participants per arm for 80% power and 1,186 participants per arm for 90% power. Planning for 75% of the observed effect gives 1,575 participants per arm for 80% power and 2,108 participants per arm for 90% power. Planning for 50% of the observed effect gives 3,542 participants per arm for 80% power and 4,742 participants per arm for 90% power.

The 80% power column means the planned study would have an 80% chance of detecting the specified effect at the stated significance level if the assumptions held and that effect were the true effect. The 90% column expresses the corresponding higher target probability. The calculations illustrate that smaller effects need more participants to detect reliably: the assumed effect is reduced across the planning scenarios, and the required participants per arm increase.

These figures are not observed power. They are hypothetical planning calculations derived from the observed estimate, not evidence about what the completed trial was designed to detect. They also do not account for any design features or analysis choices that are not reported in the registry record.

13. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

n is the number of participants in each arm, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = -1.100; pooled standard deviation σ = 8.262.
2. n = 2 × (1.96 + 0.842)² × 8.262² / -1.100² = 885.5, rounded up to 886 participants per arm for 80% power.

The smaller-effect rows in the table above repeat the same calculation with the effect multiplied by 0.75 and 0.5 (for ratios, applied to the logarithm of the ratio).

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
delta <- -1.1                      # observed difference in means
sigma <- 8.2615827781364                     # 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(1308619)
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 = 886 (80% power), 1,186 (90% power)
 75% of observed effect: n per arm = 1,575 (80% power), 2,108 (90% power)
 50% of observed effect: n per arm = 3,542 (80% power), 4,742 (90% power)
power.t.test: 886.4 
Simulated power at n = 886 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. Multiplicity, Missing Data and Analysis Populations

The registry record does not report how multiplicity was handled. This matters because the trial listed a primary outcome and several secondary outcomes, and the objective also included assessing a possible relationship between clinical effects and inflammatory markers. When several hypotheses are assessed, the chance of obtaining at least one apparently unusual result can increase. Statistical plans may address this through prespecified testing hierarchies or adjustment procedures, but whether either approach was used is not reported in the registry record.

The posted CEA comparison is an unadjusted recalculation. Its p-value should therefore not be interpreted as if it were adjusted for all outcomes or comparisons in the study. The registry lists biochemical-marker and IGA outcomes, but numerical results for them are not reported in the registry record. Their absence prevents a complete review of the secondary outcome pattern and does not establish that the outcomes were not measured.

Missing-data methods are not reported in the registry record. The record does not explain whether all randomized participants contributed to each endpoint, how missing week 12 measurements were handled, or whether sensitivity analyses were conducted. The group sample sizes attached to the posted endpoint are not, by themselves, enough to establish the analysis population or explain any exclusions.

The analysis population is also not reported in the registry record. It is not possible to determine from the posted summaries whether the primary comparison used all randomized participants, participants with observed outcomes, or another defined population. Likewise, covariate adjustment, model specification, and the treatment of protocol deviations are not reported. These omissions matter because analysis choices can affect estimates, standard errors, and the interpretation of an unadjusted comparison.

The registry lists zero reported analyses. Consequently, no sponsor-reported statistical plan or detailed inferential analysis is available in the record. The unadjusted recalculations offer a limited comparison of posted summaries, but they cannot substitute for a prespecified analysis or resolve questions about multiplicity, missing data, and population definitions.

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 3% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: chest pain (1.2%), spontaneous abortion (1.2%).

The registry posts serious adverse event counts for participants at risk in each group. In the Oracea® group, 2 of 84 participants were reported with serious adverse events; in the placebo group, 0 of 86 were reported with serious adverse events. The registry lists chest pain and spontaneous abortion among the serious-event terms, each with a reported frequency of 1.2%. These counts and terms describe events recorded during the study; they do not establish that a study treatment caused an event.

Other adverse events were reported for 8 of 84 participants in the Oracea® group and 6 of 86 participants in the placebo group. These are counts of participants affected, not counts of all event episodes. The registry record does not report deaths. It also does not provide enough information to interpret event timing, severity beyond the serious classification, relatedness assessments, or differences in exposure duration. Small event counts are inherently limited for comparing uncommon outcomes, so the posted figures should be read descriptively rather than as a precise estimate of comparative safety.

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

The primary result describes average change in inflammatory lesion counts from baseline to week 12 in the randomized groups. Both group means were negative, and the Oracea® group had a numerically more negative mean change. The unadjusted recalculated between-group estimate was -1.1 lesions, with a confidence interval that includes zero. These data therefore leave substantial uncertainty about the size and direction of the average group difference.

The result does not show that the groups are equivalent. Demonstrating equivalence would require a prespecified margin and an analysis designed to test that question; neither is reported in the registry record. Nor does a p-value above a conventional threshold prove the absence of an effect. It indicates that the observed summary data do not provide strong evidence against the tested null under the unadjusted calculation's assumptions.

The result also does not establish whether changes in lesion counts are connected to changes in skin inflammatory markers. Although the registry objective refers to a possible correlation and the listed outcomes include biochemical markers, numerical marker results and a correlation analysis are not reported in the registry record. Likewise, the available numerical results do not support conclusions about the listed IGA outcome.

Statistical significance and clinical importance are different questions. The registry does not state a threshold for a clinically meaningful difference in lesion counts, so the estimated contrast cannot be classified against such a threshold. The confidence interval communicates uncertainty about the mean difference, but it does not determine the value of a change for an individual participant.

These findings should be understood as a limited description of the posted results, not as medical advice or a treatment recommendation. Interpretation is constrained by the absence of reported analysis details, the lack of numerical results for some listed outcomes, and the uncertainty in the unadjusted primary comparison.

17. Why This Trial Matters Statistically

This trial illustrates why a randomized comparison should be interpreted through the between-group contrast, rather than by focusing on change within each group alone. Both groups had negative mean changes, but the inferential question is whether their average changes differ and how precisely that difference is estimated. Here the estimated contrast is small relative to the uncertainty expressed by its confidence interval.

It also shows why a point estimate is not sufficient for judging the strength of evidence. The estimate of -1.1 lesions gives a concise description of the observed group difference, while the interval from -3.581 to 1.381 shows that the data remain compatible with a broad range of values. Reporting both helps prevent a single estimate from being mistaken for a precise or definitive result.

The trial's stated interest in clinical outcomes and inflammatory markers raises an additional statistical distinction. Comparing treatment groups on an outcome is not the same as assessing whether two measures are correlated. A correlation analysis and complete marker results would be needed to evaluate that part of the research question; they are not reported in the registry record.

Finally, the record demonstrates the importance of a transparent statistical plan. Without the original sample-size justification, analysis population, missing-data approach, and multiplicity procedure, readers cannot assess how the posted results relate to prespecified decisions. Recalculated summary comparisons can be informative, but they do not replace those missing details or a fully reported analysis.

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 does not report the original sample-size justification, so the planning illustrations derived from the observed effect cannot establish whether the completed study was adequately sized for its intended question. The record also does not report the planned analysis population, missing-data handling, or the protocol's statistical analysis plan. These omissions limit assessment of whether the posted group summaries reflect the intended primary analysis.

Only limited numerical secondary results are posted. Although biochemical-marker and IGA outcomes are listed, their numerical results are not reported in the registry record. This leaves the study's biomarker objective and several secondary questions difficult to evaluate. The record also does not report a correlation analysis connecting clinical change with inflammatory markers.

The primary inferential comparison is an unadjusted recalculation from summary statistics, rather than a sponsor-reported model or adjusted analysis. The registry does not state whether any covariates, stratification factors, or sensitivity analyses were used. The result therefore cannot address the potential influence of those choices or of missing outcome data.

The confidence interval for the primary contrast includes zero and covers estimates in either direction. The registry provides no threshold for a clinically meaningful change in lesion counts, which limits interpretation of the estimate's practical importance. The secondary analysis is also subject to uncertainty about multiplicity, because no adjustment procedure or endpoint hierarchy is reported.

Finally, the adverse-event summaries are descriptive and contain limited information about event timing, treatment relatedness, or exposure. The registry record reports no deaths, and the small serious-event counts do not permit precise comparisons of uncommon events.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Evaluation of Rosacea-related Inflammatory Biochemical Markers in Adult Skin When Treated With Oracea® vs Placebo — NCT01308619.
• Registry record last updated 2022-08-01; status last verified 2014-07.
• Results first posted 2014-08-05.
• 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

NCT01308619 is a completed Phase 4, randomized, double-blind, parallel-group, placebo-controlled study sponsored by Galderma R&D. It enrolled 170 adults with papulopustular rosacea and compared daily Oracea®—doxycycline 40 mg, comprising 30 mg immediate-release and 10 mg delayed-release beads—with placebo.

The primary outcome was mean change in inflammatory lesion counts from baseline to week 12. The posted group means were -4.3 for Oracea® and -3.2 for placebo; the unadjusted recalculated mean difference was -1.1, with a confidence interval spanning zero. Numerical results for some listed secondary outcomes and details of the original analysis plan are not reported in the registry record.