Study of NTx®-265: Human Chorionic Gonadotropin (hCG) and Epoetin Alfa (EPO) in Acute Ischemic Stroke Patients: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study of NTx®-265: Human Chorionic Gonadotropin (hCG) and Epoetin Alfa (EPO) in Acute Ischemic Stroke Patients (NCT00938314), a randomized phase 2 study. The primary outcome is National Institutes of Health Stroke Scale (NIHSS) Change From Baseline at Day 90.

2. Clinical Question

3. Trial Design

The registry record identifies NCT00938314 as a phase IIb, prospective, randomized, double-blind, placebo-controlled, multicenter, dose-escalation study. Its official title gives the study name REGENESIS-LED. The design is parallel: participants were assigned to one of three NTx®-265 dose groups or to saline placebo. The record lists 96 participants enrolled and gives the status as terminated. It lists the study start as 2009-08 and primary completion as 2010-04; a reason for termination is not reported in the registry record.

The planned treatment sequence combined hCG and EPO. The hCG dose and schedule were the same across active groups, while the EPO dose varied across low-, medium-, and high-dose groups. The saline-placebo arm was the comparator. The registry record does not report the randomization ratio, allocation concealment procedures, or details of how blinding was maintained. It also does not report why the study was terminated or whether termination affected the timing or completeness of outcome collection.

The primary outcome was NIHSS change from baseline at Day 90. The posted analysis population is described as all randomized patients who received at least one dose of study drug, which is a modified Intent-to-Treat definition. For this outcome, the reported group sizes are 24 in each arm. Enrollment and outcome-analysis counts are not interchangeable in general; the record gives the endpoint-specific counts alongside the enrollment total. The registry lists additional functional and neurological outcomes, including measures assessed at Day 30 and Day 90. The record does not report the original statistical analysis plan or the original sample-size justification.

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.

Cohort 1

Cohort 2

Cohort 3

Analysis population for the primary outcome, as defined in the registry: The analysis was conducted using a modified Intent-to-Treat population, defined as all randomized patients who received at least one dose of study drug.

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

6. Primary Endpoint

The registry lists the primary outcome as National Institutes of Health Stroke Scale (NIHSS) Change From Baseline at Day 90, measured over Baseline and Day 90.

The primary endpoint is mean change from baseline to Day 90 on the National Institutes of Health Stroke Scale (NIHSS). The registry describes the NIHSS as a systematic assessment that quantitatively measures stroke-related neurological deficit. Scores range from 0, described as no deficit, to 42, described as dead. The outcome therefore expresses change in a measured score over time, rather than a count of participants meeting a categorical response definition.

In general, a continuous score can retain information about the range of measurements among participants, while a response endpoint reduces results to categories such as meeting or not meeting a threshold. A mean summarizes the group’s average observed change, and a standard deviation describes the spread of individual scores around that mean. Those summaries do not show each participant’s outcome or the shape of the score distribution.

The Day 90 time point gives a common endpoint for comparing the four groups after baseline measurement. The NIHSS is used in this study to represent neurological status; the registry lists separate measures of function and other neurological outcomes as secondary endpoints. The primary outcome data should be interpreted as group-level score changes, not as a direct description of every participant’s recovery or experience. The registry record does not report a minimum clinically important difference or a threshold for interpreting the size of a mean change.

7. Results Posted in the Registry

• NTx®-265 Low Dose: mean 6.79 versus 7.17 on control; difference -0.38 (95% CI -2.77 to 2.01), standardized effect d = -0.09; z-test p = 0.756.
• NTx®-265 Medium Dose: mean 6.50 versus 7.17 on control; difference -0.67 (95% CI -3.15 to 1.81), standardized effect d = -0.15; z-test p = 0.597.
• NTx®-265 High Dose: mean 6.08 versus 7.17 on control; difference -1.09 (95% CI -3.24 to 1.06), standardized effect d = -0.29; z-test p = 0.320.

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.

NIHSS Change From Baseline at Day 30

• 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:
  • NTx®-265 Low Dose: mean 4.67 versus 5.33 on control; difference -0.66 (95% CI -2.91 to 1.59), standardized effect d = -0.17; z-test p = 0.565.
  • NTx®-265 Medium Dose: mean 4.29 versus 5.33 on control; difference -1.04 (95% CI -2.94 to 0.86), standardized effect d = -0.31; z-test p = 0.282.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between NTx®-265 Low Dose and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between NTx®-265 Medium Dose and the control. The interval gives the range of effects that remain compatible with the data.

Barthel Index at Day 90

• 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:
  • NTx®-265 Low Dose: mean 68.18 versus 90.89 on control; difference -22.71 (95% CI -36.34 to -9.08), standardized effect d = -0.97; z-test p = 0.001.
  • NTx®-265 Medium Dose: mean 80.17 versus 90.89 on control; difference -10.72 (95% CI -22.39 to 0.95), standardized effect d = -0.60; z-test p = 0.072.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for NTx®-265 Low Dose than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between NTx®-265 Medium Dose and the control. The interval gives the range of effects that remain compatible with the data.

Boston Naming Test (BNT) Change From Baseline at Day 90

• 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:
  • NTx®-265 Low Dose: mean 3.93 versus 3.69 on control; difference 0.24 (95% CI -2.40 to 2.88), standardized effect d = 0.07; z-test p = 0.858.
  • NTx®-265 Medium Dose: mean 4.17 versus 3.69 on control; difference 0.48 (95% CI -2.64 to 3.60), standardized effect d = 0.12; z-test p = 0.763.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between NTx®-265 Low Dose and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between NTx®-265 Medium Dose and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes cover additional neurological and functional measures, including NIHSS at Day 30, the Modified Rankin Scale, Barthel Index, arm function, gait velocity, naming, and line cancellation. The registry lists these outcomes alongside the Day 90 primary NIHSS measure. The posted secondary data do not form one uniform pattern across all measures: means and contrasts vary by outcome, and the numbers contributing to different measures are not the same. Some outcomes have fewer observations than the primary endpoint, which adds uncertainty and makes direct comparison across outcomes difficult.

In general, secondary endpoints can help describe whether a primary result is accompanied by similar patterns in other domains. They do not automatically confirm or overturn the primary result, especially when many outcomes and treatment contrasts are examined. The Day 90 primary result itself is uncertain, with unadjusted intervals spanning zero. Secondary findings should therefore be considered supplementary context rather than independent confirmation of a treatment effect. They measure different aspects of outcome and are not interchangeable with the primary NIHSS change.

Unadjusted secondary comparisons carry less weight because multiple outcomes and pairwise contrasts create more opportunities for chance findings. The registry record does not report a multiplicity adjustment or a hierarchy specifying which secondary outcomes should receive confirmatory interpretation. In addition, formal sponsor analyses for the posted secondary continuous outcomes are not reported in the registry record; the available contrasts are recalculations from summary statistics where presented. A reader should therefore focus on the overall pattern and uncertainty, rather than treating an isolated unadjusted result as definitive evidence.

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

• NIHSS Response >=4 at Day 90
• NIHSS Change From Baseline at Day 30
• Modified Rankin Scale (mRS) Response <=2 at Day 90
• Barthel Index at Day 90
• Action Research Arm Test (ARAT) Change From Baseline at Day 90
• Gait Velocity Test Change From Baseline at Day 90
• Boston Naming Test (BNT) Change From Baseline at Day 90
• Line Cancellation Test Change From Baseline at Day 90

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous, and the posted summaries give the mean and standard deviation in each arm. In general, a mean is the arithmetic average of observed values; it gives a compact description of the group but does not reveal the distribution of individual outcomes. A standard deviation describes how dispersed observations are around the mean. It is not the uncertainty of the mean itself. In this study, the reported primary standard deviations range from 3.3 to 4.53 across the four groups.

What does a mean difference represent?

The pairwise mean difference compares an active dose-group mean with the saline-placebo mean. The recalculated contrasts use the posted summaries and are unadjusted. A negative estimate means that the active-arm mean change is numerically lower than the placebo-arm mean change under the subtraction convention used for these contrasts. That numerical direction does not by itself establish whether the result is better or worse clinically; the registry record does not report an interpretation threshold for the change score. An adjusted analysis might differ from a simple comparison if it accounted for baseline values or other variables, but such an analysis is not reported in the registry record.

Why does the confidence interval matter?

In general, a confidence interval describes the range of effect estimates reasonably compatible with the observed data and the method used to calculate the interval. It shows precision as well as direction and magnitude. Intervals that include zero do not establish that the true difference is exactly zero; they indicate that the data do not sharply distinguish a zero difference from some nonzero differences under that method. The primary pairwise intervals are wide and include zero. Their breadth reflects uncertainty in the estimated differences, rather than proof that the arms are identical.

How should p-values be read?

In general, a p-value measures how unusual data at least as incompatible with a specified null hypothesis would be if that null model and the test assumptions were correct. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of an effect. The values 0.756, 0.597, and 0.32 are unadjusted results from the simple recalculations, not sponsor-reported inferential analyses. They should be read with the estimated differences and intervals, not in isolation. The registry record does not report a formal primary-endpoint p-value from the sponsor.

What does unadjusted mean?

General explanation: unadjusted comparisons assess each contrast without accounting for the existence of other comparisons or other outcome measures. When several groups and outcomes are examined, the chance of seeing at least one apparently unusual result can increase. A multiplicity procedure can alter how evidence is judged, but the registry record does not report a multiplicity strategy. The presented p-values and intervals therefore do not represent a reported correction for multiple comparisons.

Why can variability affect precision?

In general, greater variability among individual measurements makes a group mean less precise when the sample size is unchanged. Standard deviations describe observed spread, while the confidence interval for a difference captures uncertainty in the contrast. The primary endpoint standard deviations are not small relative to the reported mean differences, and the group sizes are limited. This context helps explain why the confidence intervals cover a broad range of values. It does not supply a new estimate of effect or alter the posted results.

What analysis population was used?

The registry describes the primary analysis as modified Intent-to-Treat: randomized participants who received at least one dose of study drug. In general, an analysis population definition determines which participants contribute to the reported result. A modified Intent-to-Treat population differs from an all-randomized population when randomized participants who received no dose are excluded. The record does not report the number of such participants, their outcomes, or a separate all-randomized analysis. It also does not report the specific missing-data method, assumptions about missing outcomes, or sensitivity analyses.

The trial has four groups, but each recalculated contrast compares one dose group with placebo. The pairwise results should not be mistaken for an overall test comparing all four groups or for a trend analysis across doses. Neither an overall test nor a dose-trend analysis is reported in the registry record. The endpoint summaries and recalculated contrasts are useful for describing what the posted data contain, but they do not replace a prespecified statistical analysis.

11. Confidence Intervals and Precision

Precision concerns how narrowly the data locate a plausible value for a group difference. The primary endpoint point estimates are -0.38 for low dose, -0.67 for medium dose, and -1.09 for high dose versus saline placebo. Their confidence intervals are -2.773 to 2.013, -3.152 to 1.812, and -3.24 to 1.06. All three intervals include zero and extend to both negative and positive values. As a result, the point estimates alone give an incomplete account: the intervals show considerable uncertainty about the direction and magnitude of each difference.

In general, a confidence interval is not a guarantee that the true value lies inside the interval, nor is it a range of individual participant outcomes. It reflects the uncertainty of an estimated group contrast under the calculation’s assumptions. The intervals were recalculated from posted summary statistics; sponsor-reported confidence intervals for the primary endpoint are not reported in the registry record. The recalculations are unadjusted and do not incorporate a reported multiplicity correction or covariate adjustment.

The primary arm sizes are 24 per group, and the standard deviations range from 3.3 to 4.53. These data provide a useful sense of why the estimates are not highly precise: the group means are estimated from limited samples in the presence of individual variation. Precision should not be confused with whether a result is important, and an interval that includes zero is not proof of no difference. It indicates that the posted data leave substantial uncertainty about the true contrast. The registry record does not provide a prespecified clinically important difference against which to judge whether parts of these intervals would be meaningful.

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 illustrations translate an observed pairwise effect into hypothetical numbers of participants needed per arm under stated assumptions. They are not the original trial’s design calculation: the original sample-size justification and its assumptions are not reported in the registry record. The illustrations use a two-sided significance level of 0.05, equal allocation between the two arms being compared, and a normal approximation. The effect to detect is set at 100%, 75%, or 50% of the observed effect. For these continuous outcomes, the figures are participants per arm, not a total across both arms and not total events.

The 80% power column describes the participant count per arm that the illustration associates with an 80% chance of detecting the specified effect under those assumptions, if the assumed effect and analysis conditions hold. The 90% power column gives the corresponding count for a higher target chance of detection. These are planning concepts, not guarantees about what a future study would find. Smaller effects require more participants because a smaller group difference is harder to distinguish from random variation. The rows that plan for 75% or 50% of the observed effect therefore generally require larger group sizes than planning for the full observed effect.

The observed effect can itself be uncertain, particularly in a small study. The displayed planning counts are consequently illustrations based on the observed estimates, not a validated design recommendation. This is not observed power: it does not measure the probability that the completed trial detected an effect after the results were known. It also does not establish that the original trial was adequately or inadequately designed. The trial’s own design assumptions are not reported in the registry record.

13. How the Sample Size Is Derived

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

Formula

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

Worked calculation for this trial

1. Observed difference Δ = -0.380; pooled standard deviation σ = 4.230.
2. n = 2 × (1.96 + 0.842)² × 4.230² / -0.380² = 1,945.2, rounded up to 1,946 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 <- -0.38                      # observed difference in means
sigma <- 4.23001182031445                     # 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(938314)
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 = 1,946 (80% power), 2,605 (90% power)
 75% of observed effect: n per arm = 3,459 (80% power), 4,630 (90% power)
 50% of observed effect: n per arm = 7,781 (80% power), 10,417 (90% power)
power.t.test: 1946.1 
Simulated power at n = 1,946 per arm: 0.799 (20000 replicates)

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

14. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when investigators assess several outcomes, treatment groups, or contrasts. In general, each additional statistical test creates another opportunity for a result to appear noteworthy by chance, even when there is no underlying difference. A prespecified strategy can address this issue by defining a primary comparison, ordering tests, or adjusting the threshold for inference. The registry record identifies a primary NIHSS outcome and lists numerous secondary outcomes, but a multiplicity strategy is not reported in the registry record. The recalculated pairwise p-values are unadjusted and should not be interpreted as if a family-wise correction had been applied.

Missing-data handling is also important for outcomes measured after baseline. The registry identifies a modified Intent-to-Treat population for the primary endpoint: randomized participants who received at least one dose. It gives 24 participants per group for the primary outcome, while some secondary outcomes have fewer observations. The reasons for differences in available counts, the amount and pattern of missing data, and the method used to handle missing measurements are not reported in the registry record. Imputation methods, sensitivity analyses, and assumptions about outcomes that were not observed are also not reported.

The record does not report the original statistical analysis plan, an adjusted primary analysis, covariate selection, or an overall test across the three doses and placebo. It therefore cannot establish from the posted details which analyses were prespecified or whether the posted summary comparisons correspond to the intended primary inferential procedure. The stated analysis population provides useful information, but it does not resolve questions about participants who were randomized and did not receive study drug or participants without outcome measurements. These reporting gaps limit evaluation of robustness and of how strongly the secondary results should be weighted.

15. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: cardio-respiratory arrest (8.3%), sudden cardiac death (8.3%), cardiac arrest (4.2%), cerebral vascular accident (4.2%), dyspnoea (4.2%).

The registry reports serious adverse events among 24 participants at risk in each group. Serious events affected 2 participants in the low-dose group, 4 in the medium-dose group, 3 in the high-dose group, and 2 in the saline-placebo group. For other adverse events, the record reports 9, 19, 2, and 10 participants affected in those respective groups, again with 24 at risk in each. These are counts of participants affected, not counts of every event experienced.

The serious-event terms listed include Cardio-Respiratory Arrest and Sudden Cardiac Death, each reported as 8.3%, and Cardiac Arrest, Cerebral Vascular Accident, Dyspnoea, and Gastrointestinal Hemorrhage, each reported as 4.2%. The registry does not provide enough detail in these summaries to infer causes or compare risk reliably. Death counts by group are not reported in the registry record. The figures should be read descriptively; they do not establish that a treatment caused or prevented an event, and they do not replace a fuller safety analysis.

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

The posted results describe mean NIHSS changes in four small groups and unadjusted pairwise differences calculated from those summaries. The point estimates are modest in relation to their uncertainty, and all three recalculated confidence intervals include zero. This means the data do not precisely determine the direction or magnitude of the pairwise differences. It does not show that the groups are identical, nor does it establish a difference.

The registry record describes a randomized, double-blind, placebo-controlled phase IIb study and reports that it was terminated. Its status alone does not explain why it ended; a reason is not reported in the registry record. The primary analysis uses a modified Intent-to-Treat definition rather than all randomized participants. The reason for using that population, handling of missing measurements, and sponsor’s formal primary analysis are not reported. Those limitations matter when deciding how far to extend conclusions beyond the posted group summaries.

The secondary outcomes offer additional descriptions of neurological and functional measures, but they are numerous and do not all have the same participant counts. Unadjusted findings across multiple outcomes are vulnerable to chance patterns and should not be treated as confirmatory in the absence of a reported multiplicity plan. The safety counts are also descriptive; they do not by themselves establish comparative safety or causality.

Overall, these results document what was reported for the studied participants and outcomes, with substantial uncertainty in the primary pairwise comparisons. They do not establish whether NTx®-265 is effective or ineffective, and they do not determine what would happen in other populations or settings. The record does not report a clinically important threshold for interpreting NIHSS change, detailed missing-data analyses, or the original design assumptions. Those unreported elements limit clinical and statistical interpretation.

17. Why This Trial Matters Statistically

This study illustrates why a randomized design and a clear endpoint are only part of a statistical interpretation. The primary outcome is a continuous score, and the group means make the measured changes easy to describe. Yet a mean difference without its uncertainty can be misleading. The recalculated confidence intervals show that the observed contrasts are imprecise and compatible with effects in either direction. Looking at estimates and intervals together gives a more informative account than focusing on a p-value alone.

The trial also has several dose groups and a collection of secondary measures. This creates a multiplicity problem: isolated findings among many unadjusted comparisons may arise by chance. Without a reported analysis hierarchy or adjustment, secondary patterns are better treated as exploratory context. The distinction between the primary outcome and secondary outcomes therefore matters, even when every measure is clinically interesting.

Another statistical lesson is that the analysis population and missing-data process shape the result. The registry defines a modified Intent-to-Treat population, but does not report reasons for missing observations or methods for handling them. This leaves readers unable to assess whether the analyzed participants fully represent everyone randomized. The terminated status and unreported reason add context that cannot be resolved from the endpoint summaries alone.

Finally, sample-size illustrations based on an observed effect are not evidence about the completed study’s power. They are planning scenarios whose counts depend on the assumed effect and stated calculation assumptions. Separating those illustrations from the trial’s unreported original design assumptions helps avoid interpreting a post-result calculation as proof that the study was designed to detect a particular 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.

Several limitations specific to this record affect interpretation. The trial is listed as terminated, but the reason and any consequences for recruitment, follow-up, or analysis are not reported in the registry record. The record lists 96 enrolled participants, while the primary endpoint summaries include 24 participants per arm. It does not explain whether every enrolled participant was randomized, whether any randomized participants received no study drug, or whether the endpoint counts reflect missing Day 90 measurements.

The primary comparison statistics are recalculated unadjusted contrasts from posted group means, standard deviations, and sample sizes. Sponsor-reported formal analyses are not reported in the registry record, and no original statistical analysis plan is available in the listed information. The registry does not report adjustment for baseline NIHSS, an overall comparison across all four groups, a dose-trend test, or a multiplicity strategy. The recalculated contrasts therefore cannot represent any unavailable sponsor analysis.

Secondary outcome counts vary, and the record does not give reasons for this variation or describe missing-data methods. The registry also does not report clinical thresholds for interpreting the size of NIHSS change or the original sample-size justification. Safety summaries give participant counts affected, but deaths by group are not reported in the registry record, and the event summaries do not establish cause or comparative risk. Together, these reporting limitations mean the posted findings are most informative as descriptive summaries with uncertain estimates, not as a complete account of efficacy or safety.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Study of NTx®-265: Human Chorionic Gonadotropin (hCG) and Epoetin Alfa (EPO) in Acute Ischemic Stroke Patients — NCT00938314.
• Registry record last updated 2011-11-29; status last verified 2011-11.
• Results first posted 2011-11-09.
• 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

NCT00938314 is a randomized, double-blind, placebo-controlled, parallel phase IIb study of NTx®-265 in acute ischemic stroke patients. NTx®-265 combined hCG followed by EPO at three dose levels; saline placebo was the comparator. The registry lists 96 participants enrolled and gives the study status as terminated.

The primary outcome was mean NIHSS change from baseline at Day 90, analyzed in a modified Intent-to-Treat population of randomized participants who received at least one dose. The posted summaries include 24 participants per arm. Unadjusted comparisons recalculated from those summaries have confidence intervals that include zero and are imprecise. The registry record does not report the sponsor’s formal primary analysis, original sample-size justification, multiplicity approach, or missing-data methods. Secondary outcomes and adverse-event counts provide additional descriptive context, with limitations in available detail and unequal outcome counts.