Zimura Compared to Sham in Patients With Autosomal Recessive Stargardt Disease (STGD1): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Zimura Compared to Sham in Patients With Autosomal Recessive Stargardt Disease (STGD1) (NCT03364153), a randomized phase 2 study. The primary outcome is Mean Rate of Change in the Area of Ellipsoid Zone Defect From Baseline Through Month 18.

2. Clinical Question

The clinical question concerns whether the mean rate of change in ellipsoid zone defect area from baseline through Month 18 differed between participants assigned to avacincaptad pegol and those assigned to sham. The registry describes the study population as participants with autosomal recessive Stargardt disease 1 (STGD1), also identified in the condition listing as Stargardt's Macular Dystrophy.

The registry also lists change in Best Corrected Visual Acuity (BCVA) using ETDRS letters and change in photopic or mesopic macular sensitivity measured by microperimetry at Month 18. The posted outcomes therefore cover structural imaging, visual acuity, retinal sensitivity and adverse events. They address distinct aspects of study outcomes rather than interchangeable measures. The registry record does not report a broader clinical question beyond the stated safety and efficacy evaluation.

3. Trial Design

This was a randomized, triple-masked, parallel-group Phase 2b trial. The registry lists an enrollment of 121 and a completed status. The recorded start date is 2018-01-12, and the primary completion date is 2025-03-31. The posted primary analysis includes 61.0 participants in the avacincaptad pegol arm and 58.0 in the sham arm; these outcome analysis counts should be distinguished from the registry enrollment figure.

Participants were assigned to avacincaptad pegol or matching sham, with each intervention scheduled monthly for up to 17 Months. The main outcome timeframe extends from baseline through Month 18. Randomization helps define the assigned-group comparison; masking is intended to limit the influence of treatment knowledge on trial conduct and outcome assessment. The registry identifies the study as triple-masked, but which specific roles were masked is not reported in the registry record.

The primary endpoint was analyzed in an ITT population. The registry describes this as including all randomized participants and analyzing them according to their randomized assignment, regardless of the actual study drug they may have received. The posted population description ends with an incomplete phrase about participants with either a no; its remaining detail is not reported in the registry record. The reason for any differences in the number of participants contributing to individual outcomes is also not reported in the registry record.

The registry lists three secondary outcomes: change in BCVA, change in photopic or mesopic macular sensitivity, and the number of participants with adverse events. It reports four outcome measures overall and three analyses. The registry record does not report the original sample-size justification, the planned statistical power for the trial, or the intended handling of multiplicity across outcomes. Those absences limit how far the posted results can be interpreted as a complete account of the trial's design and analysis plan.

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: Participants who met all inclusion criteria and none of the exclusion criteria were enrolled in the study.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: ITT included all participants who were randomized. Participants were analyzed according to the treatment to which they were assigned at the time of randomization regardless of the actual study drug the participant may have received during the participation in the study. Participants with either a non-missing baseline or non-missing post-baseline assessment were included.

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: Intent to Treat (ITT) included all participants who were randomized. Participants were analyzed according to the treatment to which they were assigned at the time of randomization regardless of the actual study drug the participant may have received during the participation in the study.

6. Primary Endpoint

The registry lists the primary outcome as Mean Rate of Change in the Area of Ellipsoid Zone Defect From Baseline Through Month 18, measured over Baseline to Month 18.

The primary endpoint is the mean rate of change in the area of ellipsoid zone defect from baseline through Month 18, expressed in mm^2/18 months. The defect area was measured using en face spectral domain-optical coherence tomography, and the rate of change, described as a slope, was estimated with a mixed model for repeated measures (MMRM).

This endpoint is a continuous measure of a structural feature assessed with retinal imaging. A rate of change uses observations over the stated follow-up period to estimate the pattern of the measure over time, rather than reporting only a single follow-up value. Comparing the estimated rates between assigned groups addresses whether the imaging measure changed differently over the trial period.

General statistical context: a continuous endpoint can retain information about the size of measured changes, rather than reducing results to categories such as improved or not improved. Repeated-measures methods can use observations collected at multiple times and account for the structure of measurements within participants. Those features describe the general rationale for this kind of method; the registry does not report all model specifications or assumptions.

The endpoint is an imaging measure, not a direct measure of every aspect of vision or daily function. The registry lists BCVA and macular sensitivity as separate secondary outcomes. Their presence reflects that structural imaging and functional measurements answer related but different questions. The registry record does not state a threshold for a change in ellipsoid zone defect area that would be considered clinically important.

7. Results Posted in the Registry

• Avacincaptad Pegol: mean 0.64 versus 0.66 on control; difference -0.03 (95% CI -0.33 to 0.28), standardized effect d = -0.03; z-test p = 0.866.

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 in Best Corrected Visual Acuity (BCVA) Using Early Treatment Diabetic Retinopathy Study (ETDRS) Letters From Baseline at Month 18

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard errors.
• Result:
  • Avacincaptad Pegol: mean -0.13 versus -1.34 on control; difference 1.20 (95% CI -2.08 to 4.49), standardized effect d = 0.13; z-test p = 0.473.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Avacincaptad Pegol and the control. The interval gives the range of effects that remain compatible with the data.

Change in Photopic or Mesopic Macular Sensitivity Measured by Microperimetry From Baseline at Month 18

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard errors.
• Result:
  • Avacincaptad Pegol: mean -1.16 versus -1.92 on control; difference 0.76 (95% CI -1.47 to 2.99), standardized effect d = 0.21; z-test p = 0.505.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Avacincaptad Pegol and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary outcomes address visual acuity, macular sensitivity and adverse events. The continuous visual outcomes are reported as model-based changes from baseline at Month 18. Across the continuous secondary comparisons, the estimated differences are not accompanied by confidence intervals that exclude no difference. This broad pattern does not establish that the groups were equivalent; it indicates that the posted estimates do not precisely demonstrate a separation on these outcomes.

The secondary outcomes complement the primary imaging endpoint because they measure different dimensions. Structural change in ellipsoid zone defect area, BCVA measured in ETDRS letters, and macular sensitivity measured by microperimetry are not interchangeable endpoints. Considering them together can describe a broader range of measured outcomes, but consistency across measures should not be overstated when their estimates remain uncertain and the analysis details are limited.

The microperimetry analysis includes 20.0 participants in the avacincaptad pegol arm and 19.0 in the sham arm, compared with 61.0 and 58.0 for the primary outcome. The reason for the smaller analysis counts is not reported in the registry record. This limits how confidently that secondary result can represent the full randomized population.

Unadjusted secondary results carry less weight when several outcomes are examined because the chance of observing an apparently notable result can increase with repeated testing. General statistical explanation: a multiplicity strategy can control or otherwise address that issue, but the registry record does not report whether such a strategy was prespecified or used. The secondary results are therefore best treated as supportive and descriptive, rather than as independent confirmatory evidence. The registry lists the number of participants with adverse events separately; those safety counts should not be combined with efficacy outcomes.

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

• Change in Best Corrected Visual Acuity (BCVA) Using Early Treatment Diabetic Retinopathy Study (ETDRS) Letters From Baseline at Month 18
• Change in Photopic or Mesopic Macular Sensitivity Measured by Microperimetry From Baseline at Month 18
• Number of Participants With Adverse Events (AEs)

9. Statistical Interpretation

10. Statistical Methods Explained

The primary analysis is described as a mixed model for repeated measures (MMRM). The endpoint is a rate, or slope, in the area of ellipsoid zone defect from baseline through Month 18. The reported comparison is a difference in least-squares means. This is a model-based comparison of the assigned groups, rather than merely a subtraction of unadjusted arm averages.

What does a repeated-measures model do?

General statistical explanation: repeated-measures models are designed for data in which an outcome is measured at multiple visits for the same participant. Measurements from a participant are related, so treating every measurement as though it came from a different person would generally misrepresent the data structure. A model can represent the time pattern and estimate group differences while accounting for that repeated structure. The registry identifies MMRM but does not report the complete visit schedule, covariance structure, fixed effects, or other model specifications.

Least-squares means are model-based estimates of group means. Their difference expresses the estimated contrast between assigned groups under the model. The registry reports a least-squares mean difference for the primary analysis, with an estimate of -0.026, a 95% confidence interval from -0.333 to 0.281, and p = 0.867. The registry does not report a fuller description of any model adjustment variables, so no particular covariate adjustment should be assumed.

How should the standard errors be read?

The arm-level values are reported as least-squares means with standard errors. A standard error describes the uncertainty of an estimated mean, not the spread of individual outcomes. General statistical explanation: estimates with smaller standard errors are typically more precise, all else being equal. The standard errors reported for the primary arm estimates are 0.111 for avacincaptad pegol and 0.108 for sham. They should not be confused with standard deviations or interpreted as participant-level ranges.

A confidence interval expresses a range of values compatible with the data and the analysis under its assumptions. General statistical explanation: a 95% confidence interval is produced by a procedure that, over repeated use under its assumptions, would cover the underlying value in 95% of repetitions. It is not a guarantee that the true value lies in the specific interval, and it does not assign a probability to individual values after the interval has been calculated. For this primary estimate, the reported interval extends from -0.333 to 0.281.

What does the p-value contribute?

The p-value is a measure of how unusual data at least as incompatible with a null hypothesis of no group difference would be, if that null hypothesis and the analysis assumptions were true. It is not the probability that the null hypothesis is true, nor does it measure clinical importance. The reported primary p-value is 0.867. It should be considered with the estimated difference and confidence interval, and not used as an isolated pass-or-fail label.

General statistical explanation: a wide interval can reflect limited precision, and a result that does not cross a conventional significance threshold does not prove equivalence. Demonstrating equivalence or noninferiority ordinarily requires a prespecified margin and an appropriate design and analysis. Such a margin is not reported in the registry record. Nor are interim analyses or an outcome-specific significance threshold reported.

What do the recalculated comparisons represent?

The simple unadjusted re-calculations use posted summary statistics to illustrate mean differences and uncertainty. They do not reproduce the participant-level MMRM. For the primary outcome, the recalculated mean difference is -0.026, with a confidence interval from -0.330 to 0.278 and an unadjusted p-value of 0.866. Differences between that calculation and the sponsor's model-based interval or p-value can arise because the approaches use different information and assumptions. The sponsor's reported mixed-model analysis is the trial's own analysis and should be the main reference for the primary result.

The same distinction matters for secondary outcomes. A simple calculation from posted summaries does not replace the sponsor's reported mixed-model analysis, and an unadjusted p-value does not account for testing multiple outcomes. The registry record does not provide enough detail to reconstruct every model or assess every analytic choice. The calculations are best regarded as aids to reading the summary statistics, not as a second definitive analysis.

General statistical explanation: over-dispersion occurs when observed variability is greater than a model assumes. If it is present and not handled appropriately, uncertainty estimates and tests can be misleading. The registry does not report over-dispersion as an issue for these continuous outcomes, so it should not be presumed to have occurred in this trial.

11. Confidence Intervals and Precision

The primary estimate is -0.026 mm^2/18 months, and its reported 95% confidence interval runs from -0.333 to 0.281. The interval includes both negative and positive values, as well as no difference. Thus, the estimated direction is not established precisely by the posted result. The point estimate is only one value within a broader range of values compatible with the model and data.

General statistical explanation: a confidence interval communicates precision as well as direction. A narrow interval constrains the range of plausible estimates more tightly; a wide interval leaves more uncertainty. An interval that includes no difference does not establish that there is no effect, and an interval that crosses no difference does not by itself show that effects in both directions are equally likely. Interpretation depends on the estimate, interval, study design and assumptions.

The registry reports standard errors of 0.111 for the avacincaptad pegol estimate and 0.108 for the sham estimate. Those values relate to uncertainty in the arm-level least-squares means, while the confidence interval describes uncertainty in the between-group difference. They are not measures of participant-to-participant variation. The sponsor's interval for the difference is the relevant interval for interpreting the primary comparison.

The secondary comparisons also have confidence intervals that include no difference. In particular, the macular sensitivity outcome has fewer participants contributing to its posted analysis than the primary outcome; the reason for that analysis count is not reported in the registry record. Its precision and generalizability should be considered in light of that count. The registry does not report confidence intervals for individual participant outcomes or a clinically important difference threshold for the endpoints.

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 planning figures are participants per arm, not total events. The sample-size illustration is based on the observed effect and assumes a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. It considers an effect to detect equal to the stated fraction of the observed effect. These are planning assumptions for the illustration; the trial's original design assumptions and sample-size justification are not reported in the registry record.

The 80% power column gives the illustrative number of participants per arm for a design with an 80% chance of detecting the stated effect under those assumptions, if that effect and the assumptions were true. The 90% power column gives the corresponding planning figure for a 90% chance. These are prospective design calculations, not measures of what the completed trial achieved. They are not observed power.

The rows planning for 100%, 75% and 50% of the observed effect show how the assumed effect size changes the planning requirement. In general, when the effect to be detected is smaller, more participants are needed to distinguish it from random variation under otherwise similar assumptions. The observed primary effect is close to no difference, so planning directly around that estimate produces very large illustrative counts: 16,539 participants per arm for 80% power and 22,141 for 90% power when planning for 100% of the observed effect. For 75% of the observed effect, the figures are 29,403 and 39,362; for 50%, they are 66,156 and 88,563.

These calculations are sensitive to the observed effect and are not a reconstruction of the trial's design. They should not be used to infer the original investigators' intended enrollment target, assumptions about variability, dropout allowance, or analysis plan. Those details are not reported in the registry record. The planning figures describe hypothetical designs under the stated assumptions, rather than proving that the completed trial was underpowered or that its result would change with a particular enrollment.

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 = -0.026; pooled standard deviation σ = 0.847.
2. n = 2 × (1.96 + 0.842)² × 0.847² / -0.026² = 16,538.8, rounded up to 16,539 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 <- -0.0261                      # observed difference in means
sigma <- 0.847175155503609                     # 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(3364153)
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 = 16,539 (80% power), 22,141 (90% power)
 75% of observed effect: n per arm = 29,403 (80% power), 39,362 (90% power)
 50% of observed effect: n per arm = 66,156 (80% power), 88,563 (90% power)
power.t.test: 16539.7 
Simulated power at n = 16,539 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 a mixed-model analysis of the difference in least-squares means. It gives an estimate of -0.026, a 95% confidence interval from -0.333 to 0.281, and p = 0.867. This is the analysis to use when describing the trial's reported primary result.

The simple unadjusted recalculation from arm-level summary statistics gives a mean difference of -0.026, a confidence interval from -0.330 to 0.278, and an unadjusted p-value of 0.866. Its close numerical alignment with the sponsor's estimate does not make the two analyses identical. The sponsor's analysis uses the reported mixed-model approach, whereas the recalculation is based on summary statistics and does not reproduce the full repeated-measures model.

The registry indicates no discrepancy between the posted comparison and the reported analysis. The sponsor's model-based estimate, interval and p-value therefore remain the primary basis for interpretation; the recalculation is an explanatory cross-check, not a replacement analysis. Similar distinctions apply to the secondary outcomes. The recalculated statistics do not account for details unavailable in the registry record, such as full model specifications or participant-level data.

15. Multiplicity, Missing Data and Analysis Populations

The primary endpoint and three secondary outcomes are posted, but a multiplicity strategy is not reported in the registry record. When several outcomes are tested, the interpretation of individual p-values depends partly on whether the analysis plan controlled the overall chance of false-positive findings or specified a hierarchy of testing. Without that information, the posted secondary p-values should be read as unadjusted evidence rather than as results known to meet a family-wise testing plan.

The registry record does not report interim analyses, an interim stopping rule, or the original sample-size justification. It also does not report a prespecified clinically important difference for the primary or secondary endpoints. These details matter for understanding how the analysis was planned and how the findings were intended to be interpreted; their absence from the registry record should not be filled by assumption.

The primary population is described as ITT: all randomized participants are included and analyzed according to assigned treatment regardless of the actual study drug received. That description supports an assigned-group interpretation. However, the population text ends with an incomplete statement about participants with either a no, and the remainder is not reported in the registry record. The exact treatment of missing measurements, incomplete follow-up or other analysis-population exceptions is therefore unclear.

MMRM is reported for the primary slope and for sponsor analyses of continuous outcomes, but the registry does not give complete details about how missing outcome observations were handled, what assumptions were made about missingness, or whether sensitivity analyses were performed. Those omissions limit independent assessment of the robustness of the results. The difference between the number enrolled and the numbers contributing to particular outcomes should not be attributed to withdrawals, missing data or exclusions without a reported explanation.

General statistical explanation: missing-data methods rely on assumptions about why observations are absent, and sensitivity analyses can examine how conclusions change under alternative assumptions. Multiplicity and missing-data methods are part of interpreting a trial's uncertainty, not merely technical details. The registry record does not report enough information to evaluate those aspects fully.

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: ligament rupture (1.7%), sepsis (1.7%), road traffic accident (1.6%), endophthalmitis (1.6%), hypotony of eye (1.6%).

The registry reports serious adverse events affecting 3 of 61 participants at risk in the avacincaptad pegol group and 2 of 58 participants at risk in the sham group. It also reports 1 death in the avacincaptad pegol group and 0 in the sham group. These are descriptive counts in the posted record; they do not, on their own, establish whether an event was caused by the assigned intervention.

The record separately lists other adverse events affecting 47 of 61 participants at risk in the avacincaptad pegol group and 41 of 58 participants at risk in the sham group. Serious and other adverse-event counts describe different categories and should not be conflated. The listed serious-event terms include ligament rupture, sepsis, road traffic accident, endophthalmitis, hypotony of eye and rhegmatogenous retinal detachment, with percentages reported in the registry. The record does not provide enough detail in these summary figures to infer causality, timing, severity beyond the stated category, or comparative risk.

Safety counts should be interpreted in the context of the trial population, follow-up and event definitions. The registry record does not provide a full narrative assessment of each event or enough information to determine whether observed differences reflect chance, exposure time or other factors. The counts are not a substitute for the study's detailed safety analysis.

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

The primary result describes the estimated difference between randomized groups in the rate of change in an imaging measure through Month 18. The sponsor reports a difference of -0.026 mm^2/18 months, with a 95% confidence interval from -0.333 to 0.281 and p = 0.867. The interval includes no difference and permits estimates in either direction. The posted data therefore do not define a clear between-group difference on this endpoint.

That finding is not the same as proving that the treatments have identical effects. A result with an interval including no difference can reflect uncertainty, and this interval leaves substantial room for different underlying values. Conversely, the point estimate alone should not be treated as evidence of a meaningful effect. The registry does not report a threshold for clinical importance that would allow the estimate to be categorized by such a criterion.

The trial's outcomes cover a specified population, assigned interventions and follow-up period. The primary endpoint is structural imaging; the secondary visual outcomes are separate measures. These results cannot by themselves establish effects on outcomes not reported in the registry record, or beyond the stated timeframe. The results also do not establish what would happen in populations that were not represented in the trial.

The safety counts describe events recorded in the two groups, but they do not establish that an event was caused by treatment. Nor do these summary counts provide a complete characterization of an individual's risk. No medical decision should be based on these summary statistics alone; they are a record-level description of trial results, not individualized guidance.

In statistical terms, the key message is the combination of an estimate with uncertainty, rather than a binary reading of the p-value. The primary estimate is close to no difference, but the interval is not narrow enough to rule out differences in either direction. Secondary outcomes have similar uncertainty and should be interpreted cautiously in the absence of a reported multiplicity plan.

18. Why This Trial Matters Statistically

This trial is statistically informative because it pairs a randomized, masked comparison with a repeated-measures analysis of a structural imaging endpoint. Random assignment defines the contrast between groups, while the reported ITT approach retains participants in their assigned groups regardless of the actual study drug received. These features matter when interpreting estimates as comparisons of assigned strategies rather than comparisons based on treatment received.

The reported primary estimate also illustrates why a point estimate and a p-value are not enough. The estimate is near no difference, the confidence interval extends in both directions, and the p-value is 0.867. Together, these statistics indicate that the posted analysis does not precisely resolve the direction or size of a group difference. That is a statement about the information in this result, not proof of equivalence.

The trial also illustrates the distinct roles of structural and functional outcomes. Ellipsoid zone defect area, BCVA and macular sensitivity measure different things. When their estimates are uncertain, their joint pattern may be useful context, but it does not remove the need to consider multiplicity, analysis populations and outcome-specific precision.

Finally, the registry's planning illustration makes the relationship between assumed effect size and required enrollment visible. It is not the trial's original design justification, and it is not observed power. Keeping that distinction clear prevents retrospective calculations from being mistaken for the rationale used by investigators or for a measure of the completed trial's success.

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 original sample-size justification, the trial's assumed effect size or its planned power. The available planning illustration is computed from the observed effect and cannot fill in those missing design details. It also cannot establish that enrollment was inadequate or that another enrollment target would have changed the result.

Some analysis details needed to assess the primary and secondary estimates are not reported: complete model specifications, the treatment of missing outcome measurements, sensitivity analyses, multiplicity methods, interim analyses and clinically important difference thresholds. The primary population description is incomplete after a phrase about participants with either a no. This prevents a full reconstruction of eligibility within the analysis population beyond the stated ITT definition.

The microperimetry analysis includes 20.0 participants in the avacincaptad pegol group and 19.0 in the sham group. The reason for those counts is not reported in the registry record, so they should not be attributed to a particular form of missingness or selection. The posted primary analysis counts are also distinct from the overall enrollment figure, and the record does not explain the difference.

The reported primary estimate concerns an imaging measure and a defined period from baseline through Month 18. It does not provide a direct estimate for every visual function measure or longer-term outcome. The adverse-event summary reports counts but does not supply the full event narratives, causal assessments or exposure-time details needed for a comprehensive safety comparison. These are limitations of what can be concluded from the registry record, rather than claims that the underlying trial necessarily lacked such analyses.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Zimura Compared to Sham in Patients With Autosomal Recessive Stargardt Disease (STGD1) — NCT03364153.
• Registry record last updated 2026-04-15; status last verified 2026-04.
• Results first posted 2026-03-12.
• 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

NCT03364153 is a completed, randomized, triple-masked, parallel-group Phase 2b trial comparing monthly avacincaptad pegol with matching sham in participants with autosomal recessive Stargardt disease 1. The registry lists enrollment of 121 and a primary completion date of 2025-03-31.

The primary endpoint was the mean rate of change in ellipsoid zone defect area from baseline through Month 18. The sponsor's mixed-model analysis reported a difference of -0.026 mm^2/18 months, with a 95% confidence interval from -0.333 to 0.281 and p = 0.867. The interval includes no difference and allows estimates in either direction.

Posted secondary outcomes cover BCVA, macular sensitivity and adverse events. The registry record does not report the original sample-size justification, multiplicity strategy or complete missing-data methods. The results describe the recorded outcomes and their uncertainty; they do not establish effects beyond the measured endpoints and timeframe.