A Study of Danicopan in Participants With Geographic Atrophy Secondary to Age-Related Macular Degeneration: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study of Danicopan in Participants With Geographic Atrophy Secondary to Age-Related Macular Degeneration (NCT05019521), a randomized phase 2 study. The primary outcome is Rate of Change From Baseline to Week 52 in the Square Root (Sqrt) of Total Geographic Atrophy (GA) Lesion Area in the Study Eye as Measured by Fundus Autofluorescence (FAF).

2. Clinical Question

This is a dose-finding question, rather than a comparison of a single fixed regimen with placebo over the entire planned treatment period. The primary endpoint describes the rate of change in an imaging measure, not a direct measure of how participants see or function in daily life. The study also listed retinal imaging and complement-related secondary outcomes, alongside safety and pharmacokinetic aims. The registry record identifies the study as terminated; the reason for termination is not reported in the registry record.

3. Trial Design

The registry describes a Phase 2, randomized, quadruple-masked, parallel-group, placebo-controlled dose-range-finding study. The planned treatment period was 104 weeks, following a screening period of up to 6 weeks, with a 30-day follow-up after the last dose. The posted enrollment is 365. The study start date is 2021-08-23, and primary completion is recorded as 2024-07-05. The current status is terminated.

Participants were assigned to danicopan 100 mg twice daily, danicopan 200 mg twice daily, danicopan 400 mg once daily, or matching placebo. The treatment plan allowed active-treatment participants who had at least 52 weeks of treatment to switch to the optimal dose after it was identified. Placebo participants were to be re-randomized to an active group at Week 52, or to the optimal dose if identified. These planned changes matter when interpreting later-period safety or outcome summaries: the group labels and exposure periods do not necessarily represent an unchanged treatment assignment throughout follow-up.

The primary endpoint used a Week 52 analysis and a population defined as randomized participants who received at least one dose and had any post-baseline fundus autofluorescence lesion-area data for that analysis, grouped by randomized treatment. The group sizes in the primary endpoint results therefore describe that endpoint’s analysis, not the full enrollment figure. The registry record does not report the reason for termination, the original sample-size justification, or whether the termination changed the planned analyses. Those points should not be inferred from the status alone.

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: For standardization purposes, the primary and secondary efficacy analyses were measured in the pre-specified study eye per individual participant. In this study, ocular assessments were performed in both eyes at Screening. The eye that met all eligibility criteria was designated as the study eye and the other eye was used as the fellow eye. If both eyes were eligible, the right eye was designated as the study eye.

Only the first 6 of 7 groups are shown.

Primary Evaluation Period (52 Weeks)

Reasons for not completing this period:

Secondary Evaluation Period (52 Weeks)

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: All participants in the FAS (all randomized participants who received at least 1 dose \[full or partial\] of study drug grouped by randomized treatment group) who had any post-baseline FAF GA lesion area data at the Week 52 analysis. As prespecified, data were collected and reported for the participants. Therefore, the 'Ns' reported below = number of participants analyzed regardless of which eye was evaluated.

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.

Population: Full Analysis Set (FAS) included all randomized participants who received at least 1 dose (full or partial) of study drug grouped by randomized treatment group. As prespecified, data were collected and reported for the participants. Therefore, the 'Ns' reported below = number of participants analyzed regardless of which eye was evaluated.

6. Primary Endpoint

The registry lists the primary outcome as Rate of Change From Baseline to Week 52 in the Square Root (Sqrt) of Total Geographic Atrophy (GA) Lesion Area in the Study Eye as Measured by Fundus Autofluorescence (FAF), measured over Baseline, Week 52.

The primary endpoint is the rate of change from baseline to Week 52 in the square root of total geographic atrophy lesion area in the study eye, measured using fundus autofluorescence. The registry describes fundus autofluorescence as producing high-contrast retinal images that are particularly useful for detecting atrophic areas. Images were sent to a reading center for lesion-area measurement.

The lesion area, originally measured in square millimeters, was transformed to its square root and expressed in millimeters. The square-root transformation changes the scale of the area measure; it does not turn the endpoint into a count of participants or a direct visual-function score. The registry notes that a greater affected area represents a worse outcome than a smaller affected area. The endpoint is expressed as a rate in mm/year, so the group estimates describe the estimated pace of change rather than the area at a single visit.

Repeated observations through the analysis period were used in a mixed model for repeated measures to estimate the treatment-group rates. The posted primary endpoint results give least-squares means and standard errors. These are model-based group summaries, not simple raw averages. Imaging endpoints can support consistent measurement of structural change, but they do not by themselves establish how a structural difference relates to a participant’s lived experience. The registry record does not report a threshold for a clinically important difference on this endpoint.

7. Results Posted in the Registry

• Danicopan 100 mg BID: mean 0.47 versus 0.41 on control; difference 0.06 (95% CI -0.02 to 0.14), standardized effect d = 0.25; z-test p = 0.160.
• Danicopan 200 mg BID: mean 0.39 versus 0.41 on control; difference -0.02 (95% CI -0.10 to 0.07), standardized effect d = -0.06; z-test p = 0.728.
• Danicopan 400 mg QD: mean 0.44 versus 0.41 on control; difference 0.04 (95% CI -0.05 to 0.12), standardized effect d = 0.15; z-test p = 0.387.

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 Plasma Bb Fragment of Complement Factor B (Bb) Concentration

• 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:
  • Danicopan 100 mg BID: mean -0.30 versus -0.10 on control; difference -0.20 (95% CI -0.43 to 0.03), standardized effect d = -0.30; z-test p = 0.083.
  • Danicopan 200 mg BID: mean -0.70 versus -0.10 on control; difference -0.60 (95% CI -0.86 to -0.34), standardized effect d = -0.79; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Danicopan 100 mg BID and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Danicopan 200 mg BID than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registry lists a broad set of secondary outcomes, mainly structural retinal measures assessed by fundus autofluorescence and spectral-domain optical coherence tomography, alongside a complement-related biomarker. These measures cover lesion area, retinal layers, and features of the ellipsoid zone at Week 52 and Week 104. They extend the clinical question beyond the primary Week 52 rate of change, but they are not all measures of the same biological or clinical construct.

The posted record includes a secondary analysis of change in plasma Bb fragment concentration at Week 52 before dosing. Its group summaries show variation among the active regimens and placebo, with the largest numerical separation in the 200 mg twice-daily group. This is a biomarker result, not a substitute for the primary retinal imaging endpoint. The registry lists 28 secondary outcomes, while the available posted analysis detail is not equally complete across those outcomes. A consistent overall pattern across every secondary measure cannot be established from the record.

Secondary endpoints can help describe whether different kinds of measurements move in related or contrasting ways. They may also help generate questions for future study. But interpreting many outcomes at once raises the chance of selectively emphasizing an unusual result. Without a reported multiplicity strategy, prespecified hierarchy, and full analysis details, unadjusted secondary findings carry less weight than a well-defined primary analysis. They should be considered supportive or exploratory, not independent confirmation of the primary result.

The primary and secondary outcomes also differ in scale, timing, and measurement method. Agreement between them would not automatically show that a treatment changes an outcome important to participants, and disagreement would not by itself invalidate the primary analysis. The registry record does not report a plan for integrating the secondary outcomes into a single overall conclusion.

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

• Change From Baseline to Week 104 in the Sqrt of the Total GA Lesion Area in the Study Eye as Measured by FAF
• Change From Baseline to Week 52 and Week 104 in the Total GA Lesion Area in the Study Eye as Measured by FAF
• Change From Baseline to Week 52 and Week 104 in Percent Macular Ellipsoid Zone (EZ) Total Attenuation in the Study Eye, the Fellow Eye, and Both Eyes Combined as Measured by Spectral-domain Optical Coherence Tomography (SD-OCT)
• Change From Baseline to Week 52 and Week 104 in Percent Macular EZ Partial Attenuation in the Study Eye, the Fellow Eye, and Both Eyes Combined as Measured by SD-OCT
• Change From Baseline to Week 52 and Week 104 in Outer Nuclear Layer (ONL) - Retinal Pigment Epithelium (RPE) Mean Central 1 mm Subfield Thickness in the Study Eye, the Fellow Eye, and Both Eyes Combined as Measured by SD-OCT
• Change From Baseline to Week 52 and Week 104 in ONL-RPE Mean Central Macular 2 mm Subfield Thickness in the Study Eye, the Fellow Eye, and Both Eyes Combined as Measured by SD-OCT
• Change From Baseline to Week 52 and Week 104 in Ellipsoid Zone (EZ) - (RPE) Macular Volume in the Study Eye, the Fellow Eye, and Both Eyes Combined as Measured by SD-OCT
• Change From Baseline to Week 52 and Week 104 in EZ-RPE Mean Central 1 mm Subfield Thickness in the Study Eye, the Fellow Eye, and Both Eyes Combined as Measured by SD-OCT

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous: it is a measured rate rather than a yes-or-no event. The registry reports a least-squares mean for each group and a standard error. The comparisons are mean differences between an active-treatment group and placebo. A negative difference means the active-group estimate is numerically lower than the placebo estimate on the reported scale; a positive difference means it is numerically higher. Interpretation of direction must remain tied to the endpoint’s definition and scale.

What the repeated-measures model does

General statistical explanation: a mixed model for repeated measures can use observations collected at multiple visits while estimating how the outcome changes over time and whether that pattern differs by assigned group. It accounts for the fact that measurements from the same participant are related, rather than treating every visit as if it came from a different person. The registry says the primary rate was estimated using coefficients for time and the interaction of time and treatment. In general, the interaction represents whether the estimated time pattern varies among treatment groups.

A least-squares mean is a model-based estimate, often adjusted for features included in the model. It is not necessarily the same as the arithmetic mean of all observed values. The registry record does not report the full model specification, covariates, covariance structure, or details of how incomplete longitudinal records were handled. Those omissions limit independent reproduction of the sponsor’s model-based result.

Standard errors and confidence intervals

General statistical explanation: a standard error describes the sampling uncertainty around an estimate. It is not the spread of individual participants’ measurements. A confidence interval gives a range of estimates compatible with the data and the statistical procedure, under its assumptions. A wider interval indicates less precision; a narrow interval indicates greater precision. An interval that includes no difference does not prove equality, and an interval that excludes no difference does not by itself establish clinical importance.

The recalculated comparisons use the posted group summaries and are simple unadjusted comparisons. They do not reproduce the repeated-measures model. The record marks the primary recalculation’s standard deviations as approximate, derived from reported standard errors. This approximation, and the difference between a simple comparison and the sponsor’s longitudinal model, are reasons not to expect every interval or p-value to match exactly. The record does not flag a discrepancy, but that does not make the two methods interchangeable.

Unadjusted comparisons and multiple outcomes

The three recalculated primary comparisons each contrast one danicopan regimen with placebo. Their p-values are unadjusted, meaning they are not corrected to account for considering several comparisons. General statistical explanation: when many hypotheses are examined, the chance of at least one apparently notable result can rise unless the analysis plan addresses multiplicity. Adjustment methods and hierarchical testing can change how results are interpreted. The registry record does not report a multiplicity procedure for these comparisons, so the recalculated p-values should be treated as exploratory rather than as a family-wise decision rule.

The study also registered many secondary outcomes and posted analyses beyond the primary endpoint. A collection of outcomes can provide useful descriptive context, but isolated results carry less weight when there is no clear account of prespecification, multiplicity control, or missing-data handling. The record lists the outcome domains and some results, but a complete statistical analysis plan is not reported in the registry record.

Planning calculations are not observed power

General statistical explanation: power is the probability that a specified analysis would detect an effect of a specified size under stated assumptions. A planning calculation uses an assumed effect and variability to describe a hypothetical future study design. It does not measure the probability that the completed study’s findings are correct. The displayed planning illustrations are based on the observed effect, a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. The registry record’s original design assumptions and sample-size justification are not reported. Further interpretation of these planning values is given with the sample-size reading.

11. Confidence Intervals and Precision

Precision is best assessed from the uncertainty around a difference, not from the point estimate alone. In the simple recalculations, each primary comparison has a confidence interval that spans no difference. The interval for danicopan 100 mg twice daily ranges from -0.023 to 0.141; for danicopan 200 mg twice daily, from -0.100 to 0.070; and for danicopan 400 mg once daily, from -0.047 to 0.121. These intervals are recalculated from posted summary statistics and are not the sponsor’s repeated-measures model intervals.

Because the intervals span both negative and positive differences, the recalculated estimates leave uncertainty about the direction of the difference as well as its magnitude. The 200 mg twice-daily point estimate is close to zero, but the interval also allows differences away from zero. A point estimate near zero is not proof of equivalence. Equivalence would require a prespecified margin and a suitable analysis; such a margin is not reported in the registry record.

The sponsor’s own mixed-model results report 90% confidence intervals: 100 mg twice daily, -0.010 to 0.126; 200 mg twice daily, -0.086 to 0.055; and 400 mg once daily, -0.033 to 0.106. These model-based intervals also include no difference. They should not be conflated with the recalculated intervals, which arise from a different method and use a different confidence level. Both sets are useful for understanding uncertainty, but the sponsor analysis is the registered model-based analysis.

Confidence intervals do not capture every source of uncertainty. Their usual interpretation depends on the analysis assumptions, while issues such as outcome selection, missing observations, and multiplicity require separate consideration. The registry record does not report a clinically important difference threshold for this endpoint. Consequently, statistical precision cannot be translated into a conclusion about clinical importance from these results alone.

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 these continuous-outcome comparisons, the figures are participants per arm, not total events. The stated assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The calculation uses the stated fraction of the observed effect: the full observed effect, 75% of that effect, or 50% of that effect. The trial’s own original sample-size assumptions and justification are not reported in the registry record.

The 80% power column gives an illustrative number of participants per arm for a hypothetical study to have an 80% chance of detecting the chosen effect under those assumptions. The 90% power column gives the corresponding illustration for a 90% chance. Higher target power generally requires more participants, all else equal. Smaller effects are harder to detect, so the planning figures increase when the assumed effect is reduced from the full observed effect to 75% or 50% of it. The amounts vary by comparison because the observed differences vary.

These calculations are not observed power. They are not a measure of the probability that the posted result is true, and they do not show that the completed trial was adequately or inadequately powered. The assumed effect comes from the observed estimate, which is uncertain; planning a future study around that estimate may therefore be optimistic or unstable. The plots and figures should be read as conditional illustrations, not as design recommendations or as a substitute for a prespecified sample-size rationale.

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 = 0.059; pooled standard deviation σ = 0.240.
2. n = 2 × (1.96 + 0.842)² × 0.240² / 0.059² = 260.1, rounded up to 261 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 <- 0.059                      # observed difference in means
sigma <- 0.240140785580511                     # 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(5019521)
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 = 261 (80% power), 349 (90% power)
 75% of observed effect: n per arm = 463 (80% power), 619 (90% power)
 50% of observed effect: n per arm = 1,041 (80% power), 1,393 (90% power)
power.t.test: 261 
Simulated power at n = 261 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 registry reports sponsor mixed-model comparisons of each danicopan regimen with placebo. The sponsor’s estimated differences are 0.058 for 100 mg twice daily, -0.016 for 200 mg twice daily, and 0.037 for 400 mg once daily. The associated 90% confidence intervals are -0.010 to 0.126, -0.086 to 0.055, and -0.033 to 0.106, respectively. Each interval includes no difference. The registered p-value is reported identically for all three comparisons.

The simple recalculations use posted group summary estimates and standard errors, rather than the full repeated-measures data and model. Their differences are 0.059, -0.015, and 0.037, and their unadjusted p-values are 0.16, 0.728, and 0.387. Small differences between the estimates are consistent with the fact that the methods are not the same. The recalculated intervals also use a different procedure and confidence level, so they should not be substituted for the sponsor’s intervals.

The registry record does not flag a discrepancy between the sponsor’s analysis and the recalculation. However, it does not provide enough detail to independently reproduce the sponsor’s model or explain why the same p-value appears for each comparison. The sponsor’s results are the registered model-based analysis; the recalculation is a transparent, unadjusted check based on summary statistics, not a replacement for that analysis.

15. Multiplicity, Missing Data and Analysis Populations

The study has several active-treatment comparisons against placebo and a large set of secondary outcomes. When multiple hypotheses are tested, unadjusted significance tests can produce apparently notable findings by chance more often than a single prespecified test. General statistical explanation: multiplicity procedures control or structure that risk, for example by adjusting thresholds or by testing outcomes in a prespecified order. The registry record does not report a multiplicity adjustment or a hierarchy governing the primary and secondary comparisons.

The three recalculated primary p-values are unadjusted. They therefore describe each simple comparison separately and should not be read as controlling the error rate across all three comparisons. The sponsor’s reported analysis labels the comparisons as superiority analyses, but the complete testing strategy and any adjustment are not reported in the registry record. It is not appropriate to infer a correction from the presence of a model or from the reported confidence intervals.

The registry identifies the primary endpoint population as randomized participants who received at least one dose and had any post-baseline fundus autofluorescence lesion-area data at the Week 52 analysis, grouped according to randomized treatment. That is a modified analysis population rather than an unrestricted intention-to-treat description. The record does not report the number of participants excluded from this endpoint analysis, the reasons for missing measurements, or detailed handling of missing data within the repeated-measures model.

General statistical explanation: repeated-measures models can use available observations without requiring every participant to have a measurement at every scheduled visit, but their validity depends on assumptions about the missing-data process and model specification. The registry record does not report enough detail to assess those assumptions. The termination status makes it especially important not to assume that the planned follow-up and outcome collection were completed as intended; the reason and analytic consequences of termination are not reported in the registry record. These gaps constrain how strongly the estimates can be generalized beyond the analyzed observations.

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: endophthalmitis (4.3%), cardiac failure (4.3%), sinus node dysfunction (4.3%), gastrointestinal haemorrhage (4.3%), pancreatitis acute (4.3%).

The registry reports serious adverse events separately for primary and secondary evaluation periods. During the primary evaluation period, the serious adverse event counts were 14 of 93 for danicopan 100 mg twice daily, 19 of 91 for danicopan 200 mg twice daily, 16 of 91 for danicopan 400 mg once daily, and 15 of 90 for placebo. These are counts of participants affected among the group sizes at risk for that evaluation period. They should not be added across periods or treated as counts of unique people across the whole study.

Deaths reported in the primary evaluation period were 0, 1, 0, and 3, respectively, in the same group order. The secondary evaluation period includes participants who continued danicopan and placebo participants who moved to danicopan regimens. Its groups and exposure histories differ from the original randomized comparison. For that reason, secondary-period safety counts should not be read as a continued placebo-controlled comparison.

The listed serious-event terms each have a reported frequency of 4.3%. The record does not provide enough context in this summary to determine overlap among terms or whether an event could appear in more than one category. These descriptive counts do not establish that a treatment caused an event or that groups have comparable safety. The registry record does not report a statistical comparison of these adverse-event summaries. Safety interpretation requires context about exposure, follow-up, event definitions, and the full clinical record.

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

The primary results describe estimated Week 52 rates of change in a transformed imaging measure for four randomized groups. The simple recalculations do not show a precise separation of any danicopan regimen from placebo: all recalculated confidence intervals include no difference. The sponsor’s model-based intervals also include no difference. These findings indicate uncertainty in the estimated contrasts, rather than proof that the regimens are identical.

The estimates do not establish that any regimen improves, worsens, or has no effect on participants’ vision or daily function. The endpoint is a retinal structural measure, and the registry record does not report a threshold for a clinically important difference on that scale. A statistical difference, even if established, would not alone establish meaningful benefit to participants. Conversely, failure to establish a difference in this analysis would not prove that no difference exists.

The record also includes secondary outcomes and safety summaries, but their interpretation is limited by multiple outcomes, incomplete reporting of the analysis plan, and differences in treatment exposure after Week 52. The study’s terminated status is recorded, but the reason for termination and its consequences for the planned data collection are not reported in the registry record. These details matter when considering how representative the available results are of the originally planned study.

Accordingly, the most suitable conclusion is about the evidence in the posted record: the primary contrasts are uncertain, and the summaries do not provide a definitive basis for declaring equivalence or a clinically important difference. The results should be understood as a statistical account of the analyzed endpoint and posted safety data, not as medical advice or a treatment recommendation.

18. Why This Trial Matters Statistically

This trial illustrates how dose-finding questions differ from a single comparison of one regimen with placebo. It includes multiple doses, model-based repeated measurements, a transformed imaging endpoint, and a plan to change treatment assignment after Week 52. Each feature affects the interpretation of group contrasts. A dose with a numerically different estimate is not automatically the best dose; selection would require an explicit analysis strategy and broader consideration of safety and other outcomes.

It also shows why the point estimate is only part of a result. The differences are modest in relation to their uncertainty, and the confidence intervals include no difference. Looking only at which group has the lower estimate could obscure how imprecisely that ordering is known. Reading the estimate, interval, analysis method, and multiplicity context together gives a more balanced account.

The comparison between sponsor model-based results and unadjusted recalculations is useful for statistical literacy. Similar point estimates do not make different methods interchangeable. The repeated-measures model uses a longitudinal framework, whereas the recalculation uses posted group summaries. Understanding the distinction helps prevent an arithmetic check from being mistaken for a reconstruction of the full analysis.

Finally, the registry record makes clear that endpoint interpretation depends on the population analyzed, the measurement scale, treatment changes, and missing-data assumptions. Where details are not reported, conclusions should remain bounded by what the record can support. These principles apply broadly to clinical trials that combine multiple outcomes, repeated measurements, and changing treatment exposure.

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 reason the study was terminated or how termination affected planned follow-up, outcome collection, or analysis. It records a planned 104-week treatment period and a primary Week 52 endpoint, but the available primary result should not be taken as evidence that all planned study activities were completed. The original sample-size justification and design assumptions are not reported, so the planning illustrations cannot be used to assess the trial’s original design.

The primary endpoint is an imaging measure transformed to a square-root scale. The record describes the direction of worse outcome but does not report a clinically important difference threshold or explain how changes on this scale relate to participant-perceived vision. The available analysis population requires post-baseline imaging data at Week 52, and detailed counts and reasons for missing endpoint data are not reported in the registry record.

The record does not include the full model specification, covariate list, covariance structure, or complete missing-data assumptions for the repeated-measures analysis. It also does not report a multiplicity procedure for the several active-versus-placebo comparisons and broad secondary outcome set. These omissions limit independent assessment of the sponsor analysis and the strength of conclusions from secondary findings.

Interpretation of later safety results is complicated by planned switching and re-randomization after Week 52. The secondary-period groups therefore do not represent a simple continuation of the original placebo-controlled comparison. The posted adverse-event summaries are descriptive, and the record does not report formal comparative analyses for those counts.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Study of Danicopan in Participants With Geographic Atrophy Secondary to Age-Related Macular Degeneration — NCT05019521.
• Registry record last updated 2025-09-05; status last verified 2025-08.
• Results first posted 2025-09-05.
• 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.

23. Record Summary

NCT05019521 is a randomized, quadruple-masked, parallel-group Phase 2 study of danicopan in participants with geographic atrophy secondary to age-related macular degeneration. It compared three danicopan regimens with matching placebo and was designed as a dose-finding study. The posted enrollment is 365, and the registry status is terminated.

The primary endpoint was the Week 52 rate of change in the square root of total geographic atrophy lesion area in the study eye, measured by fundus autofluorescence. The sponsor reported mixed-model comparisons; simple recalculations from posted summaries provide a separate, unadjusted view. Both sets of intervals include no difference for each active-regimen comparison. The record also lists numerous secondary outcomes and descriptive safety summaries.

The reason for termination, the original sample-size justification, complete model specifications, multiplicity procedures, and detailed missing-data handling are not reported in the registry record. Those limitations call for cautious interpretation of the posted estimates.