4 Week Correction Study in Subjects With Anemia Associated With Chronic Kidney Disease Who Are Not Undergoing Dialysis: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for 4 Week Correction Study in Subjects With Anemia Associated With Chronic Kidney Disease Who Are Not Undergoing Dialysis (NCT01587898), a randomized phase 2 study. The primary outcome is Modeled Hgb Change From Baseline Over 4 Weeks of Treatment.

2. Clinical Question

This is a short-term, dose-ranging study, not a comparison of long-term outcomes. Its primary measure is a continuous laboratory value, expressed in g/dL, and the registry describes an analysis of change over time rather than a single unmodeled measurement at the end of treatment. That distinction matters: the primary analysis used repeated hemoglobin assessments and a model, while the simple contrasts based on posted group summaries are unadjusted recalculations. Those recalculations can help describe the observed group means, but they do not replace the sponsor’s analysis.

3. Trial Design

The registry record describes a phase IIa, randomized, double-blind, placebo-controlled, parallel-group, multicenter study. Participants were assigned to placebo or once-daily GSK1278863 at 0.5 mg, 2 mg, or 5 mg, in equal proportions according to the brief summary. The planned treatment period described in the title and summary was four weeks. The trial is marked completed.

The eligibility population was restricted to people with anemia associated with chronic kidney disease who were not receiving dialysis and were not taking recombinant human erythropoietin. The stated eligible hemoglobin range was 8.5 to 11.0 g/dL. These criteria define a particular study population; they do not establish that the findings apply to people outside those criteria. The record lists total enrollment as 72, while the brief summary says approximately 68 subjects were expected. The registry record does not explain that difference.

The primary endpoint analysis population is described as the ITT population: randomized participants who received at least one dose of study medication and had a baseline and at least one corresponding on-treatment laboratory assessment. The endpoint description also says efficacy-evaluable participants needed a baseline and at least two on-treatment hemoglobin assessments, and that data up to investigational product discontinuation were included. Only participants with data available at the indicated time points were analyzed. The record does not fully reconcile these population descriptions, so they should not be treated as interchangeable.

The registry record does not report the original sample-size justification, the planned power for the trial, or the original design assumptions. The sample-size illustrations associated with the recalculations are based on observed effects and are separate from the trial’s design rationale.

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: Out of the 73 randomized participants, one participant did not receive any study medication. the remaining 72 participants were included in safety population. Another one participant had no post-randomization data and was excluded from Intent-to-treat (ITT) population (71 participants).

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The ITT population comprised of all randomized participants who received at least one dose of study medication, and had a baseline and at least one corresponding on treatment laboratory assessment. Only those participants with data available at the indicated time points were analyzed.

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 Modeled Hgb Change From Baseline Over 4 Weeks of Treatment, measured over Baseline (average of Week -2, -1 and Day 1) and Week 4.

The primary endpoint was modeled hemoglobin change from baseline over four weeks of treatment, measured in g/dL. Baseline was defined as the average of the Week -2, Week -1, and Day 1 visits. Change was calculated by subtracting baseline from the individual post-dose visit values. Hemoglobin is a continuous laboratory measure, so the endpoint describes the average modeled movement in the measure rather than a count of participants meeting a threshold.

Repeated measurements can help characterize how a continuous outcome changes over time. The registry used a random-coefficient mixed-effects linear regression model with fixed effects for baseline hemoglobin, treatment, and the interaction between treatment and day, and random effects for the intercept and slope over time. In general, a model of this kind can use the pattern of repeated observations while representing participant-level variation. The registry’s stated approach included available data up to treatment discontinuation for efficacy-evaluable participants, subject to the described assessment requirements.

The endpoint is useful for comparing the modeled short-term hemoglobin trajectories among the assigned groups. It does not by itself answer questions about longer-term outcomes, nor does a change in a laboratory measure establish a broader clinical benefit. The registry record does not report a primary endpoint confidence interval for each sponsor-estimated arm contrast or a sponsor-reported pairwise effect estimate in the material summarized for this analysis.

7. Results Posted in the Registry

• GSK1278863, 0.5 mg: mean 0.13 versus -0.15 on control; difference 0.28 (95% CI 0.13 to 0.43), standardized effect d = 1.37; z-test p = <0.001.
• GSK1278863, 2 mg: mean 0.46 versus -0.15 on control; difference 0.61 (95% CI 0.47 to 0.75), standardized effect d = 2.98; z-test p = <0.001.
• GSK1278863, 5 mg: mean 1.01 versus -0.15 on control; difference 1.16 (95% CI 1.01 to 1.31), standardized effect d = 5.04; 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.

Model-Adjusted Maximum Hgb Changes Over 4 Weeks

• 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:
  • GSK1278863, 0.5 mg: mean 0.14 versus 0.15 on control; difference -0.02 (95% CI -0.44 to 0.41), standardized effect d = -0.02; z-test p = 0.942.
  • GSK1278863, 2 mg: mean 0.47 versus 0.15 on control; difference 0.32 (95% CI -0.10 to 0.74), standardized effect d = 0.50; z-test p = 0.131.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between GSK1278863, 0.5 mg 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 GSK1278863, 2 mg and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists secondary outcomes covering model-adjusted maximum hemoglobin change, threshold-based hemoglobin increases, hemoglobin stopping criteria, and changes in hepcidin, ferritin, transferrin, and transferrin saturation. The available numerical secondary summary includes model-adjusted maximum hemoglobin change over four weeks. Numerical results for the other secondary outcomes are not reported in the registry record summarized for this analysis.

As a broad pattern, the model-adjusted maximum hemoglobin change summaries are higher in the 2 mg and 5 mg groups than in placebo, while the 0.5 mg summary is close to the placebo summary. That general pattern is relevant as context for the primary hemoglobin endpoint, but it is not the same estimand: maximum change and modeled change over time are distinct endpoint definitions. The results should therefore not be treated as interchangeable confirmations of one another.

Secondary endpoints can help describe additional dimensions of the study, but they generally carry less inferential weight than a prespecified primary endpoint when many outcomes are examined. In general, testing multiple outcomes or contrasts increases the chance of seeing apparently notable results by chance unless the analysis plan addresses multiplicity. The registry record does not report a multiplicity procedure for the listed secondary outcomes. It also does not report enough detail to determine how each secondary outcome’s analysis was prespecified or how missing measurements were handled.

The secondary findings are best understood as supplementary descriptions rather than independent proof of the primary pattern. Their interpretation should account for differing measures, analysis populations, and the potential for multiple testing. The registry record does not report numerical results for enough secondary outcomes to characterize a full cross-endpoint pattern.

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

• Model-Adjusted Maximum Hgb Changes Over 4 Weeks
• Number of Participants Achieving an Increase of 0.5, 1.0, 1.5 and 2.0 g/dL in Hgb
• Percentage of Participants Achieving an Increase of 0.5, 1.0, 1.5 and 2.0 g/dL in Hgb
• Number of Participants Who Reached Hgb Stopping Criteria
• Change From Baseline in Hepcidin at Week 2 and Week 4
• Change From Baseline in Ferritin at Week 2 and Week 4
• Change From Baseline in Transferrin at Week 2 and Week 4
• Change From Baseline in Transferrin Saturation at Week 2 and Week 4

9. Statistical Interpretation

10. Statistical Methods Explained

The primary analysis is described as a random-coefficient mixed-effects linear regression. In general, a mixed-effects model is useful when observations are collected repeatedly from participants: it can represent both overall group patterns and variation in individual starting levels or trajectories. Here, the registry says the model included fixed effects for baseline hemoglobin, treatment, and a treatment-by-day interaction. It also says random effects were fitted for the intercept and slope over time. The record does not provide the model’s full specification, such as all coding choices or covariance details, so those details should not be inferred.

What does modeled change represent?

The endpoint is not simply a single raw measurement at Week 4. It is described as modeled hemoglobin change from baseline over four weeks. Baseline was the average of Week -2, Week -1, and Day 1 values, and the individual post-dose values were expressed as changes from that baseline. In general, modeling repeated observations can use information across time and account for the fact that measurements from the same participant are related. That can make the estimate different from a comparison that uses only arm averages.

The primary summary reports a mean and standard deviation for each group. The separate recalculated pairwise comparisons use the group summaries to estimate unadjusted mean differences and confidence intervals. They are not the sponsor’s mixed-effects model contrasts. This distinction is particularly important because the record marks a discrepancy. Under that circumstance, the sponsor’s own analysis takes precedence. The recalculated contrasts are best read as a transparent, simple comparison of the posted summary statistics, not as a correction to the sponsor’s analysis.

Why can modeling and simple contrasts differ?

In general, model-based results may differ from a direct comparison of group means because the model uses repeated observations, baseline adjustment, time structure, and its assumptions about variation. The analysis population and availability of assessments can also affect the estimates. The trial record describes both an ITT population with a baseline and at least one corresponding on-treatment laboratory assessment and efficacy-evaluable participants with a baseline and at least two on-treatment hemoglobin assessments. It further says only participants with data available at indicated time points were analyzed. These descriptions signal that analyzed counts can vary, but the record does not fully explain how each population definition maps onto every displayed result.

In general, an unadjusted p-value evaluates the observed contrast under the assumptions of its comparison method without incorporating a multiplicity adjustment. A p-value is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of an effect. Here, the recalculated p-values relate to pairwise mean differences based on posted summaries. They should not be conflated with the registry’s ten listed mixed-effects p-values, for which the associated contrasts are not identified in the record.

What does over-dispersion mean in general?

For continuous outcomes, variation can reflect both true differences among participants and measurement or model variation. More variability relative to the estimated difference generally produces less precise estimates. General explanations of over-dispersion most often apply to count data, where observed variation exceeds what a simple count model expects; this trial’s primary endpoint is continuous, so that count-data concept should not be used to reinterpret the hemoglobin results. The registry reports standard deviations for the primary arm summaries, and the recalculation uses those group-level summaries.

The record also lists a model-adjusted maximum hemoglobin change as a secondary outcome, with least-squares means and standard errors. A standard error describes uncertainty in an estimated mean, whereas a standard deviation describes spread among observations; they are not interchangeable. In general, a least-squares mean is a model-based estimate, not necessarily the raw arithmetic average. These distinctions matter when reading the primary and secondary summaries together, because they use different endpoint descriptions and dispersion measures.

Finally, the record gives several reported mixed-effects p-values without a clear pairing to particular contrasts or estimates. A p-value without an identifiable estimand, contrast, and analysis context is difficult to interpret in isolation. The registry record does not report enough detail to assign those values to dose-specific comparisons, and no additional statistical plan, interim-analysis plan, or multiplicity procedure is reported in the registry record.

11. Confidence Intervals and Precision

The recalculated confidence intervals express uncertainty around simple, unadjusted differences between each active-dose group summary and placebo. For 0.5 mg, the estimated mean difference is 0.28 g/dL, with a confidence interval from 0.131 to 0.429. For 2 mg, the estimated difference is 0.611 g/dL, with a confidence interval from 0.475 to 0.747. For 5 mg, the estimated difference is 1.158 g/dL, with a confidence interval from 1.008 to 1.308.

In general, a confidence interval gives a range of values compatible with the data under the statistical method and its assumptions. A narrower interval indicates greater precision for that estimate, while a wider interval indicates more uncertainty. These intervals are recalculated from posted summary statistics and are not reported sponsor-model intervals. Because the registry record flags a discrepancy, the sponsor’s own analysis takes precedence; the recalculated intervals should not be read as replacing the model-based analysis.

The comparison intervals do not communicate all sources of uncertainty. They come from an unadjusted two-group calculation, while the primary endpoint was analyzed using a repeated-measures mixed-effects model. They also do not account for the broader issue of making several dose comparisons or examining multiple endpoints. The registry record does not report a multiplicity adjustment for these recalculated comparisons.

Precision also depends on sample size and variability. The primary analysis counts range from 13 to 18 across the four groups, and each comparison uses a limited number of participants. These counts are not necessarily the total enrolled in the trial, since the primary analysis population required available measurements. A confidence interval is not a guarantee that the true effect lies within its bounds, and it is not a statement about clinical importance. It describes statistical uncertainty for the particular estimate and method used.

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 recalculated effect, not the trial’s original sample-size plan. For these continuous-outcome comparisons, the entries are participants per arm, not total events. The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect considered is the stated fraction of the observed effect. The registry record does not report the trial’s original sample-size justification or design assumptions.

The 80% power column gives the number of participants per arm estimated, under those planning assumptions, to have an 80% chance of detecting the assumed effect at the stated significance level if that effect were the true one. The 90% power column gives the corresponding per-arm estimate for a 90% chance. These are planning concepts, not guarantees about what a future study will find.

Rows planning for 100%, 75%, or 50% of the observed effect represent different assumed effect sizes. Smaller assumed effects generally require more participants to detect with the same power and significance level. The illustrations are sensitive to the observed effect and variability, and unusually large observed effects can produce very small planning counts that may not be realistic for a future study. The columns are not evidence that the completed trial had 80% or 90% power; this is not observed power.

The 0.5 mg comparison’s illustration is based on its recalculated difference from placebo, as are the other pairwise illustrations. The sponsor’s mixed-effects analysis and the discrepancy noted in the record remain important when considering whether those observed effects are suitable planning inputs. A future design would require its own justified assumptions rather than relying automatically on the observed estimates from this small study.

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 = 0.280; pooled standard deviation σ = 0.204.
2. n = 2 × (1.96 + 0.842)² × 0.204² / 0.280² = 8.4, rounded up to 9 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 <- 0.28                      # observed difference in means
sigma <- 0.2043286947965                     # 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(1587898)
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 = 9 (80% power), 12 (90% power)
 75% of observed effect: n per arm = 15 (80% power), 20 (90% power)
 50% of observed effect: n per arm = 34 (80% power), 45 (90% power)
power.t.test: 9.4 
Simulated power at n = 9 per arm: 0.775 (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 primary analysis was a random-coefficient mixed-effects linear regression model of hemoglobin change over time. The registry lists ten results from mixed-effects linear regression, including p-values, but does not identify the contrast or estimate associated with each value in the record summarized for this analysis. It therefore does not support assigning a particular listed p-value to a specific dose-versus-placebo comparison.

The recalculated comparisons instead use the posted group means and standard deviations to form simple unadjusted pairwise mean differences, confidence intervals, and p-values. They do not reproduce the model’s use of repeated measurements, baseline hemoglobin, treatment-by-day interaction, or random effects. Consequently, these calculations should not be treated as another presentation of the sponsor’s model-based contrasts.

The record flags a discrepancy between the posted information and the recalculated results. In this situation, the sponsor’s own analysis takes precedence. The recalculated estimates remain useful as a transparent description of what follows from the arm summaries, but they cannot resolve the discrepancy or establish that the sponsor’s reported analysis is wrong. Because the record does not provide identifiable sponsor pairwise estimates and confidence intervals, a complete numerical comparison between the two approaches is not reported in the registry record.

15. Multiplicity, Missing Data and Analysis Populations

The study compares three active-dose groups with placebo and lists numerous secondary outcomes. In general, when several statistical tests are conducted, the chance of at least one apparently unusual result can increase. A multiplicity strategy may control that risk, for example by defining a testing order or adjusting the significance threshold. The registry record does not report a multiplicity adjustment or a hierarchy for the primary and secondary analyses. The recalculated p-values are unadjusted and should be interpreted with that limitation in mind.

The record reports ten mixed-effects linear regression p-values, but the associated contrasts or hypotheses are not identified in the available result descriptions. Without that mapping, the p-values cannot be assigned confidently to dose-specific comparisons or other questions. The registry record also does not report an interim-analysis plan, stopping boundaries for statistical efficacy, or a detailed statistical analysis plan. No such procedures should be inferred from the reported results.

Missing data and analysis populations are also relevant. The primary endpoint description says the ITT population consisted of randomized participants who received at least one dose and had a baseline and at least one corresponding on-treatment laboratory assessment. It separately describes efficacy-evaluable participants as those with a baseline and at least two on-treatment hemoglobin assessments, with data up to investigational product discontinuation included. It says only participants with available data at indicated time points were analyzed. The registry record does not fully clarify how these descriptions relate to every displayed primary result, nor does it report a detailed missing-data sensitivity analysis or imputation method.

In general, analyses based on observed assessments can be affected if the availability of measurements is related to participant characteristics or outcomes. That possibility cannot be evaluated from the summary information alone. Arm-specific analysis counts for the primary endpoint are reported, but the record does not provide a full account of missingness by time point or reasons for unavailable measurements. These limits do not establish that bias occurred; they constrain how completely the reported model can be assessed.

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: renal failure acute (5.6%), pancreatitis acute (5.6%), appendicitis (5.6%), hypoglycaemia (5.6%), azotaemia (5.3%).

The registry reports serious adverse events among 1 of 18 participants in the placebo group, 0 of 17 participants in the 0.5 mg group, 2 of 18 participants in the 2 mg group, and 1 of 19 participants in the 5 mg group. Deaths were reported as 0 in each group. The denominators for these safety summaries differ from some primary endpoint analysis counts, so safety and efficacy counts should not be assumed to represent identical populations.

The registry also reports other adverse events for 8 of 18 participants receiving placebo, 10 of 17 receiving 0.5 mg, 5 of 18 receiving 2 mg, and 5 of 19 receiving 5 mg. These counts describe participants in the registry’s adverse-event summaries; they do not by themselves establish whether an event was caused by study treatment. The serious-event terms listed in the record include renal failure acute, pancreatitis acute, appendicitis, hypoglycaemia, and azotaemia, each with a reported percentage of 5.6% for the first four terms and 5.3% for azotaemia.

In general, event counts from a short study with modest group sizes are imprecise and should not be treated as a reliable estimate of uncommon or delayed harms. The posted figures are descriptive, not a basis for causal conclusions or medical advice. The registry record does not provide enough detail to compare event timing, severity beyond the serious-event classification, or treatment attribution.

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

The central statistical result is a short-term comparison of modeled hemoglobin change across placebo and three GSK1278863 dose groups in a defined chronic kidney disease population. The posted group means show different estimated changes among the groups, and simple unadjusted recalculations produce positive mean differences versus placebo. Those recalculations are not the sponsor’s mixed-effects analysis, and the record flags a discrepancy; accordingly, the sponsor’s own analysis takes precedence.

The record does not permit a complete reconstruction of the sponsor’s dose-specific inferential results because the listed model-based p-values are not mapped to identifiable contrasts and the corresponding sponsor estimates and confidence intervals are not reported in the material summarized. The recalculated confidence intervals describe uncertainty under simple comparisons of group summaries, not the full repeated-measures model. They also do not address multiplicity across doses and outcomes.

The endpoint concerns hemoglobin over four weeks. It does not establish the durability of any observed change, results beyond the reported time frame, or outcomes not measured by this endpoint. It also does not establish the cause of differences between groups. Randomization and blinding are important design features, but interpretation still depends on the analysis population, available measurements, model assumptions, and completeness of reporting.

The adverse-event counts are descriptive and based on limited numbers of participants. They do not support definitive comparisons of safety between groups, especially for uncommon events. Similarly, the secondary outcome summaries provide supplementary information but do not remove the uncertainty around the primary analysis or substitute for a clearly reported multiplicity plan.

Overall, the posted summaries describe the study’s short-term laboratory findings and safety counts. They do not establish a general clinical conclusion, long-term effect, or definitive benefit-risk assessment. The statistical evidence should be read with attention to the distinction between the sponsor’s model and the unadjusted recalculations, and to the limits of the registry’s reporting.

18. Why This Trial Matters Statistically

This study illustrates why the analysis method and the endpoint definition matter as much as the arm averages. The primary outcome was a modeled change over repeated visits, analyzed with a mixed-effects regression model. A direct contrast of posted group summaries is simpler, but it answers a narrower question and does not reproduce the sponsor’s repeated-measures analysis. When a discrepancy is flagged, keeping those analyses distinct prevents an unadjusted recalculation from being mistaken for the trial’s formal result.

The study also illustrates the need for interpretable reporting of contrasts. A list of p-values without clear links to estimates, confidence intervals, and hypotheses is difficult to use for dose-specific inference. A reader needs to know what comparison was tested and how the estimate was calculated to understand the meaning and precision of a statistical result. That information is not fully reported for the sponsor’s listed analyses.

Finally, the study has multiple dose groups and a broad set of secondary outcomes. This makes multiplicity and prespecification important, while the registry record does not report a multiplicity strategy. The sample-size illustrations likewise show why planning should rely on justified assumptions: observed effects, particularly from small studies, may not be stable planning targets. These are general statistical lessons drawn from the design and reporting features of this trial, not conclusions about treatment.

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 study was short, with a four-week treatment period, so the primary endpoint addresses short-term hemoglobin change rather than longer-term patterns. The enrolled population was also specific: participants had anemia associated with chronic kidney disease, were not undergoing dialysis, and were not taking recombinant human erythropoietin. Findings from this group cannot automatically be generalized to people outside those eligibility criteria.

The registry lists enrollment of 72, while the brief summary describes approximately 68 expected subjects. The record does not explain the difference. Primary analysis counts were 18, 13, 17, and 18 across placebo and the dose groups, respectively; they differ from some safety denominators. The record describes more than one analysis-population definition and does not fully reconcile them with the displayed estimates.

The primary result is reported with group summaries, while the registry’s model-based p-values are not linked to specific contrasts in the record. The recalculated comparisons are unadjusted and are flagged as discrepant, so the sponsor’s analysis takes precedence. Sponsor pairwise estimates and confidence intervals are not reported in the available record, limiting assessment of model-based precision.

The registry record does not report the original sample-size justification, the detailed statistical analysis plan, a multiplicity strategy, an interim-analysis plan, or detailed methods for handling missing data. It also does not report numerical results for most of the listed secondary outcomes in the information available for this analysis. These reporting gaps limit evaluation of the full inferential framework; they do not establish that any particular unreported procedure was or was not used.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: 4 Week Correction Study in Subjects With Anemia Associated With Chronic Kidney Disease Who Are Not Undergoing Dialysis — NCT01587898.
• Registry record last updated 2017-11-09; status last verified 2017-08.
• Results first posted 2017-11-09.
• 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.

23. Record Summary

NCT01587898 is a completed, randomized, double-blind, placebo-controlled, parallel-group phase IIa study of once-daily GSK1278863 at 0.5 mg, 2 mg, or 5 mg versus placebo. It enrolled people with anemia associated with chronic kidney disease who were not undergoing dialysis and were not taking recombinant human erythropoietin.

The primary endpoint was modeled hemoglobin change from baseline over four weeks. The registry describes a random-coefficient mixed-effects linear regression analysis and reports group summaries. Simple unadjusted recalculations show dose-versus-placebo differences, but the record flags a discrepancy, so the sponsor’s own analysis takes precedence. The registry does not clearly map its reported model-based p-values to specific contrasts.

Secondary outcomes cover additional hemoglobin measures and laboratory markers, while the safety record reports serious and other adverse-event counts and no deaths in the groups. Missing-data details, multiplicity procedures, original design assumptions, and several secondary numerical results are not reported in the registry record.