A Trial to Evaluate the Efficacy, Durability, and Safety of KSI-301 Compared to Aflibercept in Participants With Diabetic Macular Edema (DME): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Trial to Evaluate the Efficacy, Durability, and Safety of KSI-301 Compared to Aflibercept in Participants With Diabetic Macular Edema (DME) (NCT04611152), a randomized phase 3 study. The primary outcome is Mean Change in BCVA.

2. Clinical Question

The registry describes a Phase 3 active-comparator study in treatment-naïve DME. Its central outcome is change in BCVA, a measure of visual acuity recorded using the ETDRS chart. The registry states that the BCVA letter score ranges from 0 to 100, with a gain from baseline indicating improvement in visual acuity.

The question is about the average change in the randomized groups, not whether every participant experienced the same change. The posted primary results report a mean change of 5.6 ETDRS Letters for KSI-301 and 9.5 ETDRS Letters for aflibercept. These group averages describe the observed outcome over the specified assessment period; they do not, by themselves, establish why the groups differed or what an individual participant would experience.

The registry also identifies durability, safety, injection frequency, retinal thickness, and diabetic retinopathy worsening among the study outcomes. Those outcomes provide additional context, but they do not replace the primary question about BCVA.

3. Trial Design

This was a randomized, parallel-group, Phase 3 study comparing KSI-301 with the active comparator aflibercept in participants with treatment-naïve DME. The registry lists an enrollment of 460 and classifies the study as terminated. The reason for termination is not reported in the registry record.

The registry classifies the masking as triple, while the official title describes the study as double-masked. Both descriptions indicate that masking was part of the trial, but the specific roles covered by the registry’s triple-masking classification are not reported in the registry record. The study is described as multicenter in its official title.

The treatment schedules differed. KSI-301 was administered as a 5 mg intravitreal injection every 4 weeks for 3 monthly doses, then on an individualized schedule every 8 to 24 weeks from Week 16 to Week 100. Aflibercept was administered as a 2 mg intravitreal injection every 4 weeks for 5 monthly doses, followed by dosing every 8 weeks from Week 24 to Week 100. Sham procedure is listed among the interventions, but its role in the treatment schedule is not reported in the registry record.

The primary outcome was mean change in BCVA from baseline to the average of Weeks 60 and 64. The registry defines the primary analysis population as all randomized participants who received any study treatment, analyzed according to their randomized group. It reports 230.0 participants in each primary-outcome arm. Details of the randomization procedure, the trial’s original sample-size justification, and the planned handling of missing outcome measurements are not reported in the registry record.

The registry lists a start date of 2020-09-30 and a primary completion date of 2023-05-11. These dates and the terminated status describe the study record; they do not explain the reason for termination or indicate how the trial’s original plans changed.

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: Of 670 screened participants, 460 met eligibility criteria and were randomized to treatment. Each participant contributed only one study eye to this study.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Full analysis set defined as all randomized subjects who received any study treatment (KSI-301 or aflibercept). Subjects will be analyzed according to their randomized treatment.

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 defined as all randomized subjects who received any study treatment (KSI-301 or aflibercept). Subjects will be analyzed according to their randomized treatment.

6. Primary Endpoint

The registry lists the primary outcome as Mean Change in BCVA, measured over Day 1 to Week 64.

The primary endpoint is mean change in best-corrected visual acuity (BCVA), measured in ETDRS Letters, from baseline to the average of Weeks 60 and 64. BCVA was measured using the Early Treatment Diabetic Retinopathy Study chart at a starting distance of 4 meters. The registry notes that the letter score ranges from 0 to 100 and that a gain from baseline indicates an improvement in visual acuity.

BCVA is used as a direct measure of visual acuity in this trial. A change-from-baseline endpoint compares participants’ follow-up measurements with their own baseline measurements, then summarizes those changes across a treatment group. The reported group mean therefore describes average change, while individual participants may have changes above or below that average.

The primary endpoint’s assessment period reaches the average of Weeks 60 and 64. Averaging those two visits is the endpoint definition in the registry; the results should not be read as a single-visit measurement at either week. The registry reports least-squares means and standard errors for the groups. Least-squares means are model-based group averages, and a standard error describes the uncertainty in an estimated mean rather than the spread of individual participant scores.

The endpoint is useful for comparing group-level visual-acuity change over the stated period. It does not, on its own, describe durability of treatment effect, injection burden, retinal structure, or safety. Those questions are addressed by other outcomes in the registry.

7. Results Posted in the Registry

• Aflibercept (Arm B): mean 9.50 versus 5.60 on control; difference 3.90 (95% CI 1.57 to 6.23), standardized effect d = 0.31; z-test p = 0.001.

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.

Percentage of Patients With a ≥ 2-step Worsening on the ETDRS DRSS in Studies KS301P104 and KS301P105 Combined

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Aflibercept (Arm B): 0.7% (3/437) versus 1.4% (6/433) on control; risk difference -0.7 percentage points (95% CI -2.0 to 0.6), risk ratio 0.50 (0.12–1.97); unadjusted two-proportion z-test p = 0.308.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Aflibercept (Arm B) and the control. The interval gives the range of effects that remain compatible with the data.

Mean Number of Intravitreal Injections

• 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:
  • Aflibercept (Arm B): mean 9.20 versus 5.90 on control; difference 3.30 (95% CI 3.01 to 3.59), standardized effect d = 2.08; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Aflibercept (Arm B) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Mean Change in OCT CST

• 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:
  • Aflibercept (Arm B): mean -158.50 versus -140.40 on control; difference -18.10 (95% CI -41.37 to 5.17), standardized effect d = -0.14; z-test p = 0.127.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Aflibercept (Arm B) and the control. The interval gives the range of effects that remain compatible with the data.

Across the posted secondary outcomes, results cover more than one kind of measurement: diabetic retinopathy worsening, injection frequency, and OCT central subfield thickness. Together, they address aspects of disease status, treatment burden, and retinal structure that are distinct from the primary BCVA outcome. The secondary findings therefore offer complementary context, but they do not directly answer the primary visual-acuity question.

The registry lists five secondary outcomes, and three analyses are reported. A sponsor-reported analysis is posted for the combined diabetic retinopathy worsening outcome; sponsor-reported analyses for mean injection count and OCT central subfield thickness are not reported in the registry record. The presence of a posted unadjusted recalculation for an endpoint should not be mistaken for a sponsor analysis.

General statistical explanation: when several outcomes are examined, the chance of finding at least one apparently unusual result by chance can increase, especially when tests are interpreted independently. Multiplicity methods can help control that risk, but the registry’s approach to multiplicity is not reported in the registry record. For this reason, unadjusted secondary results generally carry less weight than a prespecified primary analysis, particularly when many endpoints or comparisons are considered.

The secondary outcomes should also be interpreted in light of their own precision and measurement scale. Counts, percentages, and continuous measures have different sources of variation and use different statistical methods. An apparent pattern across these outcomes is not equivalent to a single combined treatment effect, and the registry does not report a prespecified method for combining them. They should be read as separate pieces of evidence rather than as repeated tests of the primary endpoint.

Overall, the secondary outcomes broaden the description of what was measured, but they do not resolve the discrepancy between the unadjusted primary recalculation and the sponsor’s adjusted primary analysis. Nor do they establish the reason the study was terminated, which is not reported in the registry record.

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

• Percentage of Patients With a ≥ 2-step Worsening on the ETDRS DRSS in Studies KS301P104 and KS301P105 Combined
• Percentage of Patients With a ≥ 2-step Worsening on the ETDRS DRSS in Study KS301P104
• Percentage of Patients in the KSI-301 Arm on a Q8W, Q12W, Q16W, Q20W, or Q24W Treatment Interval
• Mean Number of Intravitreal Injections
• Mean Change in OCT CST

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is continuous: it is a numerical measurement of change in BCVA. The registry reports least-squares means for each group and standard errors for those means. A least-squares mean is a model-based estimate of an average, rather than necessarily the arithmetic average of all observed values. The registry’s detailed model specification and covariates are not reported in the registry record.

What the group estimates represent

The posted primary group means are 5.6 ETDRS Letters for KSI-301 and 9.5 ETDRS Letters for aflibercept. The standard errors are 0.83 and 0.85, respectively. A standard error reflects the precision of an estimated group mean. It is not the standard deviation of individual outcomes: a standard deviation describes participant-level variation, while a standard error describes uncertainty in an estimate.

The simple recalculation compares the two posted group summaries without adjustment. It estimates the Aflibercept-minus-KSI-301 mean difference as 3.9, with a 95% confidence interval from 1.572 to 6.228 and p = 0.001. This is an unadjusted calculation based on the summaries, rather than the trial’s mixed models analysis. The recalculated pooled standard deviation is approximate because the posted primary dispersions are standard errors. The recalculation is therefore useful as a transparent comparison of the displayed summaries, but it does not reproduce the sponsor’s model.

How to read the confidence interval and p-value

A confidence interval gives a range of values compatible with the data and statistical method, under the assumptions used. A narrower interval indicates greater precision than a wider interval for the same measurement and method. A p-value describes how unusual the data would be under a specified null hypothesis, conditional on the analysis assumptions. It does not say the probability that a treatment is effective, and it does not quantify clinical importance.

The sponsor’s posted primary analysis is a mixed models analysis, reported as an adjusted mean difference of -3.8, with a 95.04% confidence interval from -5.47 to -2.17 and p = 0.416. The registry labels this a non-inferiority analysis. The reported adjusted result takes precedence over the simple unadjusted recalculation when describing the sponsor’s analysis. The non-inferiority margin, model details, and full statistical analysis plan are not reported in the registry record, so the analysis cannot be independently reconstructed from the posted summary.

Why other outcome types use different methods

Some secondary outcomes are counts or percentages rather than continuous measurements. For example, the posted diabetic retinopathy outcome counts participants with a specified worsening. A risk difference compares the proportions in two groups; its confidence interval describes uncertainty in that contrast. The sponsor reports a Cochran-Mantel-Haenszel analysis for this outcome, with a difference of weighted percentages of 0.6, a 95.04% confidence interval from -0.7 to 2, and p < 0.001. The unadjusted recalculation for the displayed counts is a different analysis and should not be substituted for the sponsor’s weighted analysis.

General statistical explanation: the Cochran-Mantel-Haenszel method can combine comparisons across strata while accounting for those strata. The registry does not report the details of the strata or the full model specification. Consequently, the reported weighted result can be described, but its exact calculation cannot be reconstructed from the summary alone.

Other secondary endpoints are continuous. Mean injection count is a count summarized by a mean, and OCT central subfield thickness is measured in microns. Their unadjusted recalculations compare group means. These simple contrasts do not necessarily correspond to any sponsor-adjusted analysis; for these outcomes, sponsor-reported comparisons are not reported in the registry record.

Why variation matters

General statistical explanation: when outcomes vary substantially among participants, an estimated group difference can be imprecise unless the study includes enough information to estimate that variation. Over-dispersion refers generally to more variation in data than a particular statistical model assumes. If a model underestimates variation, its uncertainty estimates can be too small. The registry does not report an over-dispersion assessment for these outcomes, so this concept is explanatory rather than a claim about the trial’s analyses.

For continuous outcomes, the reported standard deviations for secondary measures describe participant-level spread. For binary outcomes, uncertainty depends on the number of events and participants in each group, along with the chosen analysis. Sparse events can make estimates less stable. These general considerations help explain why estimates with similar point values can have different precision across endpoints.

The posted methods information is incomplete for reproducing the sponsor’s analyses. The registry does not report the full statistical analysis plan, covariate choices, assumptions for model fitting, missing-data methods, or the original design assumptions. Those omissions limit independent evaluation of how the reported adjusted analyses were specified, but they do not change the fact that the registry’s sponsor-reported primary analysis is the analysis that takes precedence over the recalculation.

11. Confidence Intervals and Precision

The primary unadjusted recalculation estimates an Aflibercept-minus-KSI-301 difference of 3.9 ETDRS Letters, with a 95% confidence interval from 1.572 to 6.228. The interval describes the uncertainty around this simple summary-based estimate under its statistical assumptions. It does not account for the adjustment in the sponsor’s mixed models analysis.

The sponsor’s adjusted primary result is -3.8, with a 95.04% confidence interval from -5.47 to -2.17. This interval belongs to the sponsor’s mixed models analysis, not to the unadjusted recalculation. The registry reports p = 0.416 for that analysis and labels it non-inferiority. Because the interval and p-value are tied to a particular model and hypothesis, they should not be combined with the recalculated estimate as if they were one analysis. The non-inferiority margin is not reported in the registry record.

General statistical explanation: a confidence interval expresses uncertainty about an estimated quantity, conditional on the model and assumptions. Wider intervals indicate less precision than narrower intervals for comparable estimates. An interval’s relationship to a null value can inform a statistical comparison, but interpretation also depends on which direction the contrast uses and what hypothesis was tested. A confidence interval alone does not establish clinical importance.

The sponsor reports a different confidence level for the adjusted result than the 95% interval used for the unadjusted recalculation. That distinction is important when interpreting the two results. The registry’s reported standard errors for the primary group means are 0.83 and 0.85; they quantify uncertainty in those means, not participant-to-participant variability. The full model specification and the reason for the reported confidence level are not reported in the registry record.

Precision also varies across outcomes. The OCT central subfield thickness recalculation has a 95% confidence interval from -41.37 to 5.174, while the injection-count recalculation has an interval from 3.009 to 3.591. Those intervals concern different units and different outcomes, so their widths cannot be compared as a direct measure of which endpoint matters more. The number of events, amount of variability, and method all affect precision.

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 trial’s own original sample-size assumptions are not reported in the registry record. The figures use a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation; each scenario uses the stated fraction of the observed effect as the effect to detect. These are participant counts per arm for the displayed outcomes. There are no time-to-event outcomes in these estimates that would be expressed as total event counts.

The 80% power column gives the estimated participants per arm for a hypothetical study with an 80% chance of detecting the specified effect under those planning assumptions, if the effect and assumptions were correct. The 90% power column gives the corresponding planning count for a 90% chance. These are planning probabilities for a hypothetical design, not probabilities that the observed trial result is correct. They are not observed power.

For the primary BCVA recalculation, planning for 100% of the observed effect gives estimates of 168 participants per arm for 80% power and 225 participants per arm for 90% power. Planning for 75% of the observed effect gives 298 participants per arm for 80% power and 399 for 90% power. Planning for 50% of the observed effect gives 671 participants per arm for 80% power and 898 for 90% power.

The progression from the full observed effect to smaller fractions illustrates a general principle: smaller effects are harder to distinguish from random variation, so they require more participants for the same target power, all else equal. These calculations do not demonstrate that the trial had adequate power for its original objectives. They are recalculations from the observed summaries and should not be used as a substitute for the unreported original design assumptions.

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 = 3.900; pooled standard deviation σ = 12.740.
2. n = 2 × (1.96 + 0.842)² × 12.740² / 3.900² = 167.5, rounded up to 168 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 <- 3.9                      # observed difference in means
sigma <- 12.7401334372918                     # 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(4611152)
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 = 168 (80% power), 225 (90% power)
 75% of observed effect: n per arm = 298 (80% power), 399 (90% power)
 50% of observed effect: n per arm = 671 (80% power), 898 (90% power)
power.t.test: 168.5 
Simulated power at n = 168 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 own primary analysis is reported as a mixed models analysis of adjusted mean difference. It gives a value of -3.8, a 95.04% confidence interval from -5.47 to -2.17, and p = 0.416, and is classified as a non-inferiority analysis. The registry’s simple recalculation from the posted group summaries gives an Aflibercept-minus-KSI-301 mean difference of 3.9, a 95% confidence interval from 1.572 to 6.228, and p = 0.001.

These are not two estimates from an identical method. The recalculation is an unadjusted contrast of posted summary statistics; the sponsor’s result is adjusted and comes from a mixed models analysis. The signs also use contrasts expressed in opposite directions, as reflected by the Aflibercept-minus-KSI-301 wording for the recalculation and the reported sponsor value. The registry flags a discrepancy between the recalculation and the sponsor result. The sponsor’s own analysis takes precedence.

The sponsor’s result is the appropriate result to quote when describing the sponsor-reported primary analysis. However, the registry record does not report the non-inferiority margin, the full model specification, or the complete analysis plan. Those omissions prevent an independent review of the non-inferiority criterion and full reconstruction of the adjusted estimate. The recalculation remains a descriptive check of posted group summaries, not a replacement for the sponsor’s analysis.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists six outcome measures, including the primary outcome and five secondary outcomes, and reports three analyses. Testing multiple outcomes can create a multiplicity problem: when many hypotheses are considered, the chance of at least one result appearing statistically notable by chance may rise. This is a general statistical concern, not a claim that any particular posted result is false.

The registry record does not report whether the trial used a multiplicity adjustment, a hierarchy of testing, or another procedure to control interpretation across endpoints. It also does not report the full statistical analysis plan. Without those details, the posted secondary p-values and confidence intervals should be interpreted as reported, but not assumed to have been adjusted for testing across outcomes.

Missing data are another important consideration for a longitudinal outcome assessed through Week 64. The registry defines the primary analysis population as randomized participants who received any study treatment, analyzed according to randomized group. It does not report the number of participants with observed primary endpoint data at each assessment, reasons for missing measurements, or the method used to address missing data in the primary analysis. The number randomized and the number contributing to a particular visit can differ, so the posted arm counts do not by themselves establish complete follow-up.

The registry also does not report sensitivity analyses assessing how conclusions might change under alternative assumptions about missing outcomes. Such analyses are generally used to examine whether conclusions depend strongly on assumptions about unobserved data; their absence from the registry record limits assessment of that issue.

The posted secondary analysis populations and handling of missing observations are not described in full. The combined diabetic retinopathy outcome reports denominators of 433.0 and 437.0, while the primary endpoint reports 230.0 per arm. Those values relate to different posted outcome records and should not be treated as a single common analysis population. The registry does not explain the relationship between those populations. These reporting gaps limit assessment of attrition, analysis-set consistency, and the robustness of the endpoint results.

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: diabetic foot (2.6%), myocardial infarction (2.2%), coronary artery disease (2.2%), covid-19 (2.2%), osteomyelitis (1.7%).

The registry reports serious adverse events for 61 of 230 participants in the KSI-301 group and 51 of 230 participants in the aflibercept group. It reports other adverse events for 126 of 230 participants in the KSI-301 group and 121 of 230 participants in the aflibercept group. Five deaths are reported in each group.

These are participant counts with events, not a measure of whether an event was caused by treatment. The registry’s summary does not provide the timing, duration, severity details, or individual clinical context needed to interpret each event. It also does not establish whether a participant experienced more than one event. Such details are not reported in the registry record.

The serious-event terms listed include diabetic foot at 2.6%, myocardial infarction at 2.2%, coronary artery disease at 2.2%, COVID-19 at 2.2%, osteomyelitis at 1.7%, and cellulitis at 1.7%. These listed percentages should be read as the registry’s event-term summaries; the denominator and any event-level counting rules are not specified in the posted details.

Safety counts provide descriptive information about events recorded during the study. They do not, without further analysis and context, establish a difference in risk between treatments or causation. The registry’s safety summaries should be interpreted alongside the stated group sizes and the limitations of the available event detail.

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

The posted primary group estimates describe mean BCVA change through the average of Weeks 60 and 64: 5.6 ETDRS Letters for KSI-301 and 9.5 for aflibercept. The simple unadjusted recalculation gives a difference of 3.9 in the Aflibercept-minus-KSI-301 direction. The sponsor’s own reported analysis is an adjusted mixed models result of -3.8, with a 95.04% confidence interval from -5.47 to -2.17 and p = 0.416, classified as non-inferiority. Because the sponsor analysis takes precedence and the non-inferiority margin is not reported, the registry information does not support an independent conclusion about whether a non-inferiority criterion was met.

The result does not show that every participant’s vision changed by the group average. A mean is a summary of a group, and participant outcomes can vary. The results also do not establish that any observed difference is important to participants; the registry does not provide a threshold for clinical importance.

The posted endpoint comparisons do not settle questions beyond the measured outcomes and analysis. They do not explain the study’s termination, identify the reason for any event, or show how outcomes would generalize to populations or treatment schedules not described by the trial. The registry lists the study as terminated, but the reason is not reported in the registry record.

The secondary findings provide separate information about retinal changes, injections, and safety. They are not interchangeable with BCVA, and unadjusted secondary analyses carry additional uncertainty when multiplicity handling is not reported. The primary-analysis discrepancy, absent non-inferiority margin, and limited information about missing-data methods further constrain interpretation.

Accordingly, the most precise reading is descriptive: the registry reports group-level measurements and a sponsor-reported adjusted analysis, while a simple summary-based recalculation differs. These data should not be turned into advice for individual care or a broad claim about treatment effects beyond the trial’s stated population, outcomes, and analysis.

18. Why This Trial Matters Statistically

This trial is statistically notable because it places an individualized dosing schedule for KSI-301 alongside a fixed aflibercept schedule and measures both visual acuity and treatment burden. The primary outcome is mean BCVA change, while injection frequency and retinal measures capture other dimensions of the study. Distinguishing these outcomes matters: a difference in one measurement does not automatically imply a difference in another.

The record also illustrates why adjusted analyses and simple recalculations must be kept distinct. The group summaries permit a transparent unadjusted comparison, but the sponsor reports a mixed models analysis framed as non-inferiority. Since those analyses are not identical and the registry flags a discrepancy, quoting the recalculation alone would not accurately describe the sponsor’s primary result. The non-inferiority margin and full model details are not reported, which limits independent evaluation.

Precision and planning assumptions also matter. The sample-size illustrations use observed effects and specified hypothetical planning assumptions; they do not recreate the original trial design. Smaller effects require larger planned samples for a given target power. This distinction helps prevent a post hoc planning calculation from being mistaken for evidence that the actual trial had adequate power.

Finally, multiplicity and incomplete reporting affect how confidently secondary findings can be weighed. Several outcomes cover different aspects of the study, but the approach to multiplicity, missing data, and the original sample-size justification is not reported in the registry record. These are not merely technical details: they determine how strongly an endpoint can support a conclusion and how reproducible the analysis is from the record.

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 lists the study as terminated, but the reason for termination is not reported in the registry record. That missing context means the status alone cannot explain whether termination related to results, operational issues, or another reason.

The primary sponsor analysis is labeled non-inferiority, but the non-inferiority margin is not reported in the registry record. The full statistical analysis plan, detailed model specification, and original sample-size justification are also not reported. The registry therefore does not allow an independent reconstruction of the sponsor’s primary adjusted analysis or a full assessment of its non-inferiority criterion.

The simple primary recalculation is based on posted summary statistics, not the sponsor’s model. The record flags a discrepancy, and the sponsor’s own analysis takes precedence. The recalculation should not be presented as a competing primary analysis or as a correction to the sponsor’s result.

Details about missing primary measurements, reasons for missingness, and the method used to address missing data are not reported in the registry record. The record also does not provide the complete analysis populations for every secondary endpoint or explain the differing denominators across posted outcomes. This limits assessment of attrition and consistency between analysis sets.

The registry does not report how multiplicity across outcomes was handled. Consequently, secondary results should not be treated as if they necessarily control the overall chance of false-positive findings. The full details of adverse-event timing and clinical context are also not available in the posted summaries, limiting causal interpretation of safety counts.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Trial to Evaluate the Efficacy, Durability, and Safety of KSI-301 Compared to Aflibercept in Participants With Diabetic Macular Edema (DME) — NCT04611152.
• Registry record last updated 2024-08-22; status last verified 2024-08.
• Results first posted 2024-08-22.
• 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

The registry record describes a randomized, parallel-group Phase 3 study of KSI-301 versus aflibercept in participants with treatment-naïve DME. It lists an enrollment of 460 and a terminated status. KSI-301 used an individualized dosing schedule after initial monthly doses; aflibercept followed monthly doses and then every-8-week dosing.

The primary endpoint was mean change in BCVA from baseline to the average of Weeks 60 and 64. The posted group means were 5.6 ETDRS Letters for KSI-301 and 9.5 for aflibercept. The sponsor’s adjusted mixed models result was -3.8, with a 95.04% confidence interval from -5.47 to -2.17 and p = 0.416, reported as a non-inferiority analysis. The sponsor’s analysis takes precedence over the discrepant unadjusted recalculation.

Secondary outcomes address diabetic retinopathy worsening, injection frequency, and OCT central subfield thickness. Safety summaries include serious and other adverse events and deaths. Important details—including the non-inferiority margin, original design assumptions, multiplicity approach, and missing-data methods—are not reported in the registry record.