A Trial to Evaluate the Efficacy and Safety of PQ912 in Patients With Early AD: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Trial to Evaluate the Efficacy and Safety of PQ912 in Patients With Early AD (NCT03919162), a randomized phase 2 study. The primary outcome is Phase 2A: Number of Participants With Any Adverse Event of Special Interest (AESI).

2. Clinical Question

The primary question is about safety during dose selection, not whether PQ912 improves cognition or daily function. The endpoint description explains that a Pocock safety stopping boundary applied to the active arm until dose selection. If the first cohort did not meet that boundary, the dose would be selected as safe; if a higher dose was selected, participants at lower doses would be titrated up. The endpoint therefore reflects a specified early safety period and the cohort used for the dose-selection rule. It should not be read as a complete account of safety over longer treatment.

The registry record also describes a planned stage gate to Phase 2B, with longer-term efficacy and safety assessment if the gate were reached. The posted secondary outcomes include cognitive and functional measures, but those outcomes do not change the primary endpoint’s safety focus. The reason the trial was terminated is not reported in the registry record.

3. Trial Design

This was a Phase 2A randomized, double-blind, placebo-controlled, parallel-group trial of varoglutamstat (PQ912) in patients with early Alzheimer’s disease. The registry lists triple masking and multicenter conduct. The listed enrollment is 112. The record gives a start date of 2021-11-15, a primary completion date of 2024-07-12, and a status of terminated; the reason for termination is not reported in the registry record.

The study description sets out adaptive evaluation of three dose levels, with exposure to PQ912 or placebo for a minimum of 24 weeks and preliminary evaluation of cognitive function and pharmacodynamic changes on EEG spectral analysis. It describes approximately 180 participants for Phase 2A. If the stage gate to Phase 2B were reached, the summary describes a larger study group of 414, intended to assess efficacy and longer-term safety. These are figures in the study description; the reason the listed enrollment differs from the approximate Phase 2A plan is not reported in the registry record.

For the primary safety endpoint, the record specifies Cohort A: the first 60 participants after completion of 8 weeks on the full dose, 600 mg BID. The posted arm summaries report 27 participants in the PQ912 group and 33 in the placebo group for that endpoint. This endpoint-specific cohort is not interchangeable with the enrollment figure for the whole trial.

The intervention arm description says all participants started at 150 mg BID and were up-titrated to 600 mg BID; the placebo arm received matching placebo. The details of randomization procedures, allocation concealment, and the original statistical analysis plan are not reported in the registry record. The record’s status is terminated, but the reason and any consequences for the planned stage gate are not reported in the registry record.

4. Participant Flow and Accounting

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

Before assignment: Participants were randomized 1:1 to PQ912 or matching placebo. All participants randomized to PQ912 started at 150 mg BID and were up-titrated to 600 mg BID. Therefore, all data from the participants randomized to PQ912 were collected as one single active Arm/Group and separation of doses is not applicable. Participants enrolled in Phase 2A remained in the study for seamless inclusion in the Phase 2B evaluation (up to 72 weeks). No new participants were enrolled in Phase 2B.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: All participants started at 150 mg BID and were up-titrated to 600 mg BID. As pre-specified, this endpoint presents data from first 60 participants (Cohort A) after completion of 8 weeks on full dose, 600 mg BID, because Pocock safety stopping boundary applies only until dose selection.

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: The modified intent-to-treat (mITT) population, including all randomized participants who took at least one dose of the study medication and who have a baseline assessment of the primary endpoint for phase 2B (CDR-SB)

6. Primary Endpoint

The registry lists the primary outcome as Phase 2A: Number of Participants With Any Adverse Event of Special Interest (AESI), measured over From first dose to completion of 8 weeks on the full dose (Week 16).

The primary endpoint is the number of participants with any adverse event of special interest (AESI). Its timeframe runs from first dose through completion of 8 weeks on the full originally assigned dose, identified in the endpoint description as Week 16. The record describes this as a safety evaluation period and presents the endpoint for Cohort A after 8 weeks at 600 mg BID.

A participant count is a binary-outcome summary: each participant either had at least one AESI during the defined period or did not. The endpoint is useful for monitoring safety during dose evaluation, when the protocol’s dose-selection rule depends on the active arm meeting a prespecified Pocock safety stopping boundary. The registry description says that boundary applies only until dose selection. It also says that evaluation of Cohort A alone was required for this endpoint if Cohort A did not meet the boundary.

The outcome does not describe the number of separate events per participant, their severity, or their duration. Those definitions and a list of which events counted as AESIs are not reported in the registry record. Nor does the endpoint, by itself, provide a complete measure of longer-term safety. It answers a narrower question about participants with any AESI over the specified dose-evaluation period.

7. Results Posted in the Registry

• PQ912: 3.7% (1/27) versus 6.1% (2/33) on control; risk difference -2.4 percentage points (95% CI -13.2 to 8.5), risk ratio 0.61 (0.06–6.38); unadjusted two-proportion z-test p = 0.677.

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.

Phase 2B: Key Secondary Efficacy: Change From Baseline in Cognitive Functional Composite-2 (CFC2) Score, a Cognitive Functional Composite

• 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:
  • PQ912: mean -6.69 versus -7.66 on control; difference 0.97 (95% CI -3.36 to 5.30), standardized effect d = 0.15; z-test p = 0.661.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between PQ912 and the control. The interval gives the range of effects that remain compatible with the data.

Phase 2B: Change From Baseline in Alzheimer's Disease Neuroimaging Initiative (ADNI) Battery Composite (ABC, 9-item) Score

• 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:
  • PQ912: mean -0.28 versus -0.38 on control; difference 0.10 (95% CI -0.10 to 0.30), standardized effect d = 0.32; z-test p = 0.337.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between PQ912 and the control. The interval gives the range of effects that remain compatible with the data.

Phase 2B: Change From Baseline in Functional Activities Questionnaire (FAQ)

• 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:
  • PQ912: mean 4.36 versus 4.97 on control; difference -0.61 (95% CI -4.19 to 2.97), standardized effect d = -0.11; z-test p = 0.738.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between PQ912 and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary outcomes span cognition, daily function, neuropsychiatric measures, EEG, imaging, and longer-term safety. The registry record lists 12 posted secondary outcomes, while the detailed comparative summaries include a subset. Across the three outcomes with sponsor-reported model analyses, the estimates are uncertain and the intervals include no difference. The overall pattern does not provide a clear, consistent signal of improvement across the cognitive and functional measures.

These outcomes relate to the primary result by addressing different aspects of the study. The primary endpoint is an early safety measure during dose selection; the secondary outcomes address clinical or functional change and longer-term safety. A result on one type of endpoint does not determine the result on another. The secondary results therefore add context but do not overturn or replace the primary safety finding.

Unadjusted secondary results carry less weight when many outcomes are examined. Each additional analysis creates more opportunities for apparently notable results to occur by chance, even if no true effect is present. The record includes multiple outcome measures and analyses, but the multiplicity strategy and any adjustment are not reported in the registry record. The posted p-values should thus be interpreted as individual, unadjusted evidence rather than as a single confirmatory test across all outcomes.

The trial’s terminated status, endpoint-specific group sizes, and lack of reported information about missing observations also matter when interpreting the pattern. The registry record does not explain why the study was terminated or how termination affected each outcome’s analysis. Taken together, the secondary results are exploratory context, not a basis for a firm conclusion about clinical efficacy.

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

• Phase 2B: Key Secondary Efficacy: Change From Baseline in Cognitive Functional Composite-2 (CFC2) Score, a Cognitive Functional Composite
• Phase 2B: Change From Baseline in Alzheimer's Disease Neuroimaging Initiative (ADNI) Battery Composite (ABC, 9-item) Score
• Phase 2B: Change From Baseline in Quantitative Electroencephalogram (qEEG)
• Phase 2B: Change From Baseline in Functional Activities Questionnaire (FAQ)
• Phase 2B: Change From Baseline in Alzheimer's Disease Assessment Scale - Cognitive Subscale (ADAS-Cog-13)
• Phase 2B: Change From Baseline in Neuropsychiatric Inventory (NPI)
• Phase 2B: Assessment of the Longer-term Safety and Tolerability of PQ912 as Measured by Rates of All Treatment-emergent Serious Adverse Events (SAEs)
• Phase 2B: Assessment of the Longer-term Safety and Tolerability of PQ912 as Measured by Suicidality on the Columbia-Suicide Severity Rating Scale (C-SSRS)

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is binary at the participant level: an AESI was either recorded during the specified safety period or was not. The posted arm summaries give the event count and the number at risk in each group. A risk difference expresses the difference in the observed proportions between the PQ912 and placebo groups. A negative estimate in this comparison means the observed proportion was lower in the PQ912 group; it does not by itself establish a real treatment effect.

The reported risk difference is -0.024. Its interval, from -0.132 to 0.085, communicates uncertainty around that estimate. Because the interval includes zero, the posted data are compatible with no difference as well as with differences in either direction. The unadjusted p-value is 0.677. A p-value describes how unusual data at least this discrepant would be under a specified no-difference model; it is not the probability that the null hypothesis is true and does not quantify the size or clinical importance of a difference.

The registry record also reports risk ratio and odds ratio estimates for this comparison. These are alternative ways to express a binary-outcome contrast, but with few events their estimates can be unstable. The risk difference is often easier to interpret in absolute terms because it compares the proportions directly. None of these measures resolves the uncertainty from the small number of endpoint events.

The primary endpoint’s Pocock safety stopping boundary belongs to the trial’s dose-selection procedure. In general, a stopping boundary is a rule for interpreting safety information during a planned decision process. The endpoint description says this boundary applied only until dose selection and explains how participants at lower doses would be titrated if a higher dose were selected. The actual boundary value and the results of any formal boundary assessment are not reported in the registry record, so no claim about whether the rule was crossed can be made from the posted summary alone.

The secondary outcomes are continuous measures reported as least-squares means with standard errors. A least-squares mean is a model-based group estimate; it can account for features specified in the fitted model. The exact covariates and model specification are not reported in the registry record. The posted arm means and standard errors support simple unadjusted recalculations, while sponsor-reported mixed-model analyses are listed separately for the three secondary outcomes with reported analyses. Those model-based estimates are the sponsor’s analyses and should not be conflated with unadjusted calculations.

For the Cognitive Functional Composite-2 (CFC2), the sponsor’s mixed-model difference in least-squares means is 0.969, with a 95% confidence interval from -3.345 to 5.238 and p = 0.653. For the ADNI Battery Composite (ABC, 9-item), the reported difference is 0.100, with a 95% confidence interval from -0.103 to 0.303 and p = 0.324. For the Functional Activities Questionnaire (FAQ), the reported difference is -0.60, with a 95% confidence interval from -4.22 to 3.01 and p = 0.738. Each interval includes zero, indicating that the sponsor-reported model results do not distinguish a difference from no difference at the stated interval level. The analyses are labeled superiority analyses in the record.

Standard errors describe the sampling uncertainty of an estimate under the model used; they are not the same as the spread of individual participant outcomes. A confidence interval combines an estimate and its uncertainty to show a range of values compatible with the data under the analysis. Wider intervals indicate less precision. These concepts do not correct for bias from missing observations, limitations in the analysis population, or selective reporting.

Over-dispersion is a general issue for count or binary data when variability exceeds that expected under a simple model. It can make standard errors too small if the model does not accommodate the extra variability. The primary endpoint is based on few events, but the registry record does not report a dispersion assessment or a model for over-dispersion. No claim about whether over-dispersion was assessed is therefore warranted.

The sponsor’s original sample-size justification, planned statistical analysis details, interim analyses, and multiplicity strategy are not reported in the registry record. The separate planning illustrations use the stated assumptions described with those figures; they should not be mistaken for the trial’s original design calculations. Planning calculations cannot make a small observed dataset more precise or substitute for a prespecified analysis plan.

11. Confidence Intervals and Precision

Precision depends on both the estimated effect and the uncertainty around it. For the primary AESI comparison, the risk difference is -0.024 and its interval extends from -0.132 to 0.085. The interval spans zero, so the result does not isolate a direction of difference. Its width also shows that the data do not pin down the magnitude closely. This is especially relevant because the endpoint was observed in only 1 participant in the PQ912 group and 2 in the placebo group.

The primary interval’s confidence level is not reported in the registry record. It should therefore be read as the posted interval without assigning it a confidence percentage. The unadjusted p-value of 0.677 likewise does not supply a measure of precision; it addresses a different question about compatibility with a no-difference model.

For the three secondary outcomes with sponsor-reported analyses, the registry labels the intervals as 95% confidence intervals. Each includes zero: the CFC2 interval ranges from -3.345 to 5.238; the ABC interval ranges from -0.103 to 0.303; and the FAQ interval ranges from -4.22 to 3.01. These ranges show that the estimates remain uncertain and encompass both directions of difference. Their units differ, so the widths should not be compared as if they were on a common scale.

Small endpoint-specific groups and standard errors contribute to uncertainty, while model choices and missing observations can also affect precision. The registry record does not report enough detail on missing-data handling or model specification to assess those influences fully. An interval that includes zero does not prove equivalence, and an estimate near zero does not rule out effects that the data estimate imprecisely.

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 for the binary and continuous outcomes; they are not total participants across the trial. The study description also includes a planned stage-gate study group, but that is separate from these calculations. There are no time-to-event planning figures in the outcomes; in general, time-to-event planning figures can be expressed as total events rather than participants.

The calculations use a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. They use the observed effect as a reference and consider detecting the stated fraction of that effect. The rows for 100%, 75%, and 50% of the observed effect therefore represent different assumed target effects, not different observed trial results.

The 80% power column gives the participants per arm that the planning calculation estimates would be needed for an 80% chance of detecting the assumed effect under those assumptions. The 90% column gives the corresponding planning estimate for a 90% chance. Greater planned power requires more participants under the same assumptions. Likewise, smaller effects need more participants to detect than larger effects, which is why planning for 75% or 50% of the observed effect produces larger requirements than planning for the full observed effect.

These figures are planning illustrations based on the observed effects, not observed power. The original trial’s own sample-size assumptions and justification are not reported in the registry record. In particular, the illustrations do not show that the study was designed around the posted results or that the planned stage-gate enrollment was achieved.

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, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.061; treatment proportion p₁ = 0.037; average p̄ = 0.049.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.3048 = 0.5973.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.3043 = 0.2561.
4. n = (0.5973 + 0.2561)² / (-0.0236)² = 1,311.1, rounded up to 1,312 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
p0 <- 0.0606060606060606                          # control proportion
p1 <- 0.037037037037037                          # treatment proportion
n_per_arm <- function(power, frac = 1) {
  q1 <- p0 + (p1 - p0) * frac               # smaller effect = fraction of the observed difference
  pbar <- (p0 + q1) / 2
  z_b <- qnorm(power)
  ceiling(round((z_a * sqrt(2 * pbar * (1 - pbar)) + z_b * sqrt(p0 * (1 - p0) + q1 * (1 - q1)))^2 / (q1 - p0)^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 (unrounded n per arm)
cat("power.prop.test:", round(power.prop.test(p1 = p0, p2 = p1, power = 0.80)$n, 1), "\n")

# Simulation: how often does the z-test reject at the 80%-power sample size?
set.seed(3919162)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 1,312 (80% power), 1,755 (90% power)
 75% of observed effect: n per arm = 2,465 (80% power), 3,300 (90% power)
 50% of observed effect: n per arm = 5,846 (80% power), 7,825 (90% power)
power.prop.test: 1311.1 
Simulated power at n = 1,312 per arm: 0.806 (20000 replicates)

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

14. Multiplicity, Missing Data and Analysis Populations

The registry record lists multiple outcomes and analyses, including 12 posted secondary outcomes and 9 analyses. When investigators examine multiple outcomes, the chance of at least one apparently favorable result can increase. Statistical methods can address this through prespecified testing sequences or multiplicity adjustments, but the planned approach is not reported in the registry record. The listed secondary p-values should therefore be treated as unadjusted unless an adjustment is explicitly stated; no such adjustment is described for the sponsor-reported results.

The record does not report the full statistical analysis plan, the analysis population definitions, or the handling of missing data. It is therefore not possible to establish from the registry record whether analyses used an intention-to-treat population, a per-protocol population, or another defined set. The outcome-specific participant counts differ across the posted summaries, but the reasons for those differences and the amount or pattern of missing data are not reported in the registry record.

Missing-data methods can affect estimates when some measurements are unavailable, particularly if missingness is related to health status, treatment, or outcome. Mixed models can use available observations under assumptions about the missing-data process, but the exact model, covariates, and assumptions used for these sponsor analyses are not reported in the registry record. No particular missing-data method should be inferred.

The primary endpoint description states that Cohort A was used for the safety endpoint because the Pocock stopping boundary applied until dose selection. That endpoint-specific population is described, but the record does not report a full account of analysis populations for every outcome. Interim analyses beyond the described safety boundary, procedures for multiplicity, and any formal consequences of termination are also not reported in the registry record. These omissions limit assessment of whether the analyses followed a prespecified confirmatory plan.

15. 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: pneumonia (3.8%), metabolic encephalopathy (1.9%), hemorrhage intracranial (1.9%), transient ischaemic attack (1.9%), sepsis (1.9%).

The serious adverse event summaries report 11 affected participants among 53 at risk in the PQ912 group and 6 among 56 at risk in the placebo group. The registry also reports 2 deaths in the PQ912 group and 0 in the placebo group. These are descriptive counts; they do not establish that an event was caused by the assigned intervention. The record does not provide a comparative statistical analysis for these summaries in the material reported.

For other adverse events, the record reports 46 affected participants among 53 at risk in the PQ912 group and 47 among 56 at risk in the placebo group. Serious events and other events are separate summary categories, and their counts should not be combined. Event duration, severity detail, and participant-level overlap are not reported in the registry record.

The listed serious-event terms include pneumonia at 3.8%, metabolic encephalopathy at 1.9%, hemorrhage intracranial at 1.9%, transient ischaemic attack at 1.9%, sepsis at 1.9%, and urinary tract infection staphylococcal at 1.9%. The record does not specify an arm for each listed term in these summaries. These data describe recorded events; they do not establish comparative risk or causation.

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

The primary result is a comparison of participants with any AESI during the specified safety period in Cohort A. The observed counts are low, and the risk-difference interval includes zero and extends in both directions. The data do not establish a clear difference between PQ912 and placebo for this endpoint. They also do not establish that the groups have equivalent safety, because a non-significant result is not proof of equivalence.

The secondary outcomes offer limited information about cognition and function. The sponsor-reported estimates for the three outcomes with detailed analyses have intervals that include no difference. This does not establish that PQ912 improved those outcomes, and it does not rule out effects that the available data estimate imprecisely. These findings should not be treated as proof that the intervention does or does not work.

The study description distinguishes a Phase 2A dose-evaluation stage from a possible Phase 2B stage gate. The registry status is terminated, and the reason for termination and the effect on the planned development stages are not reported in the registry record. The listed enrollment and endpoint-specific group sizes should be interpreted in their respective contexts rather than assumed to represent the same analysis population.

Safety event counts are descriptive and do not on their own establish causation. Longer-term safety outcomes are listed among the Phase 2B outcomes, but the registry record does not provide a complete account of follow-up or missing observations. The record also does not report the complete statistical plan, the multiplicity strategy, or the rationale for the final enrollment. Those limitations constrain any broader inference from the posted results.

In short, the posted data are compatible with uncertainty about both the size and direction of group differences. They are not a basis for clinical recommendations. Their value is in describing the observed safety counts and the limited comparative results while making clear how much remains unresolved.

17. Why This Trial Matters Statistically

This trial illustrates why the endpoint and its analysis population must be read together. The primary result concerns Cohort A during a defined safety window tied to dose selection, rather than every participant over the full study period. The record’s broader enrollment figure, the Phase 2A description, and the endpoint-specific group counts answer different questions and should not be collapsed into one denominator.

It also illustrates the impact of sparse binary outcomes. When only a few participants experience an endpoint, the estimate can be highly uncertain even when the observed group counts differ. The risk difference and its interval communicate both the direction of the point estimate and the limited precision; the p-value alone cannot do that.

The trial’s stage-gate structure is another important statistical feature. A safety rule governing dose selection has a different role from a confirmatory efficacy analysis. The record describes the stopping-boundary process, but does not report its numerical boundary or the formal assessment result. Keeping the operational safety decision distinct from claims about cognitive benefit is essential.

Finally, multiple secondary outcomes, a terminated status, and unreported details about missing data and multiplicity restrict how much can be inferred. This is a useful example of reading registry results as evidence with a specific scope—not as a complete account of the protocol, analysis decisions, or treatment effect.

18. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

The primary endpoint is based on Cohort A and a specific period after reaching the full dose. It is not a full-trial summary of all adverse events or longer-term safety. The registry record does not report the AESI event definitions, the numerical Pocock boundary, or the formal boundary assessment result. This limits independent evaluation of the dose-selection safety process.

The primary event counts are small, and the resulting risk-difference interval is broad. The confidence level for that interval is not reported in the registry record. The primary comparison also has no sponsor-reported model analysis in the posted results described. The reason that the listed enrollment is 112 rather than the approximately 180 participants described for Phase 2A is not reported in the registry record.

The trial is marked terminated, but the reason, timing, and consequences for the planned stage gate are not reported in the registry record. The secondary results are labeled Phase 2B and include small outcome-specific groups. The record does not explain how termination affected their follow-up, analysis populations, or availability.

Important analytic details are absent: the full statistical analysis plan, multiplicity approach, missing-data methods, and definitions of analysis populations are not reported in the registry record. The exact mixed-model specifications for secondary results are also not reported. These limitations make it difficult to assess robustness, selection effects, and whether the posted analyses were confirmatory or exploratory.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: A Trial to Evaluate the Efficacy and Safety of PQ912 in Patients With Early AD — NCT03919162.
• Registry record last updated 2025-12-12; status last verified 2025-12.
• Results first posted 2025-12-12.
• 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.

22. Record Summary

The registry record describes a randomized, double-blind, placebo-controlled Phase 2A trial of PQ912 (varoglutamstat) in early Alzheimer’s disease, with a stage gate to a possible Phase 2B study. It lists enrollment of 112 and a terminated status. The reason for termination is not reported in the registry record.

The primary endpoint counts participants with any AESI during the specified safety evaluation period in Cohort A. The posted counts are 1 among 27 in the PQ912 group and 2 among 33 in the placebo group. The unadjusted risk difference is -0.024, with an interval from -0.132 to 0.085 and p = 0.677. The result is uncertain and does not establish a clear group difference.

The registry also posts secondary cognitive and functional outcomes, including sponsor-reported mixed-model analyses for three outcomes. Their reported intervals include zero. Missing-data handling, multiplicity strategy, and the reason for termination are not reported in the registry record, limiting broader interpretation.