Strategies Using Darbepoetin Alfa to Avoid Transfusions in Chronic Kidney Disease: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Strategies Using Darbepoetin Alfa to Avoid Transfusions in Chronic Kidney Disease (NCT01652872), a randomized phase 3 study. The primary outcome is Percentage of Participants in Receipt of 1 or More RBC Transfusions.

2. Clinical Question

The clinical contrast is between two dosing approaches using darbepoetin alfa, not between darbepoetin alfa and no active treatment throughout the study. The registry lists placebo as an intervention, and the fixed-dose arm description refers to placebo when treatment is withheld under its stated exception. The principal outcome is a binary event: whether a participant had one or more transfusions during the defined evaluation period. The posted results therefore address the frequency of participants experiencing any transfusion, rather than the number of transfusions per participant or the timing of the first transfusion. Those are listed as secondary outcomes, but their numerical results are not reported in the registry record.

3. Trial Design

This was a phase 3, multicenter, randomized, parallel-group study. The brief summary describes a 1:1 allocation and a double-blind design. The registry classifies masking as triple; the record does not explain which parties were masked, so the two descriptions cannot be reconciled further from the registry record. The trial status is completed. The listed start date is 2012-07-30, and the primary completion date is 2017-10-19.

Participants were assigned to hemoglobin-based titration or a fixed-dose strategy. In the titration group, darbepoetin alfa was given subcutaneously every 4 weeks, with doses adjusted according to the visit hemoglobin concentration, its corresponding rate of rise, and the previously assigned dose. The brief summary states a target of maintaining hemoglobin at or above 10.0 g/dL. In the fixed-dose group, the assigned dose was intended to remain the same for the 96-week treatment period. The arm description records an exception for hemoglobin greater than 12.0 g/dL, when darbepoetin alfa was withheld and placebo was used; the description ends before the details are complete.

The study planned follow-up for approximately 2 years from randomization. The primary endpoint timeframe is described as randomization until the end of study, up to week 101, with an on-treatment censoring rule. The reported analysis population was not simply every randomized participant: the full analysis set included those who were randomized and received at least one dose of investigational product. Each posted primary outcome group has 377 participants. The registry record does not report the original sample-size justification, the intended statistical analysis plan in full, or whether interim analyses were planned or conducted.

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 in a 1:1 ratio to 1 of 2 darbepoetin alfa dosing strategies (hemoglobin \[Hb\]-based titration group or fixed dose group). Randomization was stratified by red blood cell (RBC) transfusion received within 12 months prior to randomization (yes/no) and site practice setting (nephrology/non-nephrology).

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The full analysis set included all randomized participants who received at least 1 dose of investigational product.

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 Percentage of Participants in Receipt of 1 or More RBC Transfusions, measured over From randomization until the end of study, up to week 101..

The primary endpoint is the percentage of participants who received at least one red blood cell transfusion during the evaluation period. It records whether the event occurred for each participant, not how many units were transfused or how many separate transfusions occurred. The record lists mean number of units transfused and time to first transfusion as secondary outcomes, distinguishing those questions from the primary one.

A binary endpoint can be useful when the study question concerns the proportion of participants who experience an event. It gives a direct summary of how common that event was in each randomized group over the specified observation period. Here, the event is receipt of one or more transfusions, and the endpoint is evaluated on an on-treatment basis. Participants were censored at the last dose plus 3 months or at the end of study, whichever occurred earlier; consequently, the result is tied to that evaluation and censoring definition rather than to an unrestricted assessment of every event after randomization.

The registry reports the endpoint as a percentage and gives a 95% confidence interval for each group. A group percentage describes the observed event frequency in that group. The confidence interval conveys uncertainty around the estimated frequency. The comparative interpretation also depends on the difference between group estimates and its confidence interval, not only on whether either group’s percentage seems large or small in isolation.

7. Results Posted in the Registry

• Fixed Dose Group: 24.1% (91/377) versus 24.4% (92/377) on control; risk difference -0.3 percentage points (95% CI -6.4 to 5.9), risk ratio 0.99 (0.77–1.27); unadjusted two-proportion z-test p = 0.932.

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.

Mean Achieved Hb Concentration While Receiving Investigational Product

• 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:
  • Fixed Dose Group: mean 9.41 versus 9.71 on control; difference -0.30 (95% CI -0.43 to -0.17), standardized effect d = -0.34; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Fixed Dose Group than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes cover several related but distinct questions: mean number of red blood cell units transfused, time to first transfusion, achieved hemoglobin concentration while receiving investigational product, and cumulative darbepoetin alfa dose. This breadth can add context to a binary primary endpoint, because it distinguishes whether any transfusion occurred from the amount and timing of transfusion, and relates the dosing strategies to hemoglobin and medication exposure.

The numerical secondary result available for interpretation is achieved hemoglobin concentration from week 13 until the end of study, up to week 101. The registry record lists the group means and a comparison for this outcome. The results for mean units transfused, time to first transfusion, and cumulative dose are not reported in the registry record. Their outcome names alone do not establish whether those measures differed between groups or how precisely they were estimated.

The available secondary information should be considered alongside, rather than as a replacement for, the primary transfusion result. A secondary measure can illuminate a different aspect of the treatment strategies, but it does not change what the primary endpoint measures. The record does not report a multiplicity-adjustment procedure or a hierarchy governing confirmatory interpretation of secondary outcomes. When multiple outcomes are examined, the chance of at least one apparently notable result can increase unless the analysis plan accounts for that multiplicity. Accordingly, unadjusted secondary findings generally carry less confirmatory weight than a prespecified primary analysis. The registry does not report whether the secondary analyses were prespecified in a detailed statistical analysis plan or how their multiplicity was handled.

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

• Mean Number of Units of RBC Transfused
• Time to First RBC Transfusion
• Mean Achieved Hb Concentration While Receiving Investigational Product
• Geometric Mean Cumulative Dose of Darbepoetin Alfa Per 4 Weeks

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary because each participant either received at least one red blood cell transfusion during the evaluation period or did not. The group percentages estimate the probability of that event in each treatment group under the endpoint definition. The posted counts, 92 of 377 and 91 of 377, are the event counts underlying the group summaries. Randomization supports a comparative interpretation by assigning participants to strategies, but it does not eliminate uncertainty in the estimated difference.

What does a risk difference express?

A risk difference subtracts one group’s event probability from the other’s. The recalculated estimate is -0.003 for fixed dose relative to hemoglobin-based titration. A negative value means the observed proportion was lower in the fixed-dose group under this subtraction order. The 95% confidence interval, -0.064 to 0.059, gives a range of values compatible with the data under the calculation’s assumptions. Because the interval spans zero, the data do not provide a clear distinction between a lower event probability, no difference, and a higher event probability. A confidence interval is not a guarantee that the true effect lies within its limits; it describes the uncertainty of an estimation procedure under repeated use of its assumptions.

How do relative measures differ?

A risk ratio compares event probabilities by division rather than subtraction. A value at the no-relative-difference point represents equal risks in the two groups. The recalculated risk ratio is 0.989, with a 95% confidence interval from 0.769 to 1.273. This interval includes the no-difference value and permits relative effects in either direction. The registry also reports a Cochran-Mantel-Haenszel risk ratio of 0.998, with an interval from 0.776 to 1.285. The registry does not identify the stratification factors used for that analysis, so no further description of its adjustment can be given.

An odds ratio is another relative measure, based on the odds of an event rather than the event probability itself. The recalculated odds ratio is 0.986, with a 95% confidence interval from 0.707 to 1.375. As with the risk ratio, the interval includes the value associated with no difference. Odds ratios and risk ratios are not interchangeable in general, even when both describe the same binary endpoint. They should be interpreted according to their own scales.

What does the p-value add?

The recalculated unadjusted p-value is 0.932. A p-value describes how incompatible the observed data are with a specified null hypothesis, assuming the model and analysis choices are appropriate. It is not the probability that the null hypothesis is true, and it does not measure the size or importance of an effect. A large p-value does not establish equivalence or prove the absence of an effect. The sponsor-reported analysis does not include a p-value in the posted record.

The word unadjusted describes the recalculation as a direct comparison without covariate or stratification adjustment. It should not be confused with adjustment for multiple testing. The sponsor’s risk-ratio method is identified as Cochran-Mantel-Haenszel, while the treatment-difference method is not specified in the registry record. The unadjusted re-calculation and sponsor analysis therefore need not produce identical estimates, even though they address the same broad comparison.

Why does the endpoint definition matter?

The event window starts at randomization and ends at the end of study, up to week 101, but the analysis applies an on-treatment censoring rule. Participants were censored at the last dose plus 3 months or the end of study, whichever was earlier. Censoring determines which follow-up time contributes to an analysis; it is not the same as observing that no event occurred. The registry record does not report additional details about how missing outcome information was handled, how censoring was incorporated into the treatment-difference calculation, or whether sensitivity analyses were conducted.

The primary analysis population is the full analysis set: randomized participants who received at least one dose of investigational product. That definition excludes randomized participants who did not receive a dose, if any, and it differs from a strict all-randomized analysis population. The record does not give the number of randomized participants excluded from this set or the reasons for any exclusions. These population and follow-up definitions are part of the estimand being described; results apply to the posted analysis and should not be detached from those definitions.

11. Confidence Intervals and Precision

The 95% confidence intervals for the primary group percentages are 20.07 to 28.74 for hemoglobin-based titration and 19.82 to 28.46 for fixed dose. The intervals overlap substantially, consistent with the similar observed percentages. However, overlap between separate group intervals is not itself the formal test of a treatment difference. The comparative interval is more directly informative: the recalculated risk difference is -0.003, with a 95% confidence interval from -0.064 to 0.059.

That comparative interval includes zero and extends in both directions. It therefore allows for a lower event proportion with fixed dose, little or no difference, or a higher proportion with fixed dose. The point estimate is close to zero, but the uncertainty is wide relative to that estimate. The confidence interval should be read as a precision statement, not as evidence that every value within it is equally likely or as a range that contains all plausible effects with certainty.

The registry’s treatment-difference interval, -6.39 to 5.85, also spans zero. Its reported risk-ratio interval, 0.776 to 1.285, spans the no-relative-difference value. The recalculated risk-ratio interval, 0.769 to 1.273, does so as well. The exact intervals differ because the sponsor and recalculation use different stated approaches. Taken together, these results do not pin down a small difference with high precision and do not establish equivalence. The registry record does not report a prespecified equivalence or non-inferiority margin against which to assess the interval.

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 80% power and participants per arm for 90% power. They are illustrations based on the observed primary effect, not the original trial’s design calculation; the registry record does not report the trial’s own sample-size assumptions. The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each planning scenario uses the stated fraction of the observed effect as the effect to detect.

For planning at 100% of the observed effect, the figures are 410,076 participants per arm for 80% power and 548,975 participants per arm for 90% power. At 75% of the observed effect, they are 729,701 per arm and 976,861 per arm, respectively. At 50% of the observed effect, they are 1,643,347 per arm and 2,199,974 per arm. Smaller effects require more participants because a subtler difference is harder to distinguish from sampling variation under the same planning assumptions.

The 80% column describes a planning target in which the assumed effect would be detected by the specified test in 80% of repeated studies, if the assumptions held. The 90% column uses a higher probability of detection and consequently calls for a larger planned group size. These are not observed power calculations for the completed trial. They do not indicate the probability that the trial’s conclusion is correct, and they do not replace the confidence interval for interpreting precision. The figures are particularly sensitive to the small observed risk difference, so they should be read as conditional illustrations rather than recommendations for a future 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, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.244; treatment proportion p₁ = 0.241; average p̄ = 0.243.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6063 = 1.1883.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6063 = 0.5103.
4. n = (1.1883 + 0.5103)² / (-0.0027)² = 410,075.3, rounded up to 410,076 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 <- 0.244031830238727                          # control proportion
p1 <- 0.241379310344828                          # 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(1652872)
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 = 410,076 (80% power), 548,975 (90% power)
 75% of observed effect: n per arm = 729,701 (80% power), 976,861 (90% power)
 50% of observed effect: n per arm = 1,643,347 (80% power), 2,199,974 (90% power)
power.prop.test: 410075.3 
Simulated power at n = 410,076 per arm: 0.802 (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. Analyses Reported by the Sponsor

The sponsor-reported treatment difference is -0.27, with a 95% confidence interval from -6.39 to 5.85. The sponsor also reports a Cochran-Mantel-Haenszel risk ratio of 0.998, with a 95% confidence interval from 0.776 to 1.285. Both reported intervals include the no-difference value on their respective scales. The sponsor does not report a p-value for either analysis in the registry record.

The recalculated unadjusted risk difference is -0.003, with a 95% confidence interval from -0.064 to 0.059 and an unadjusted p-value of 0.932. The recalculated risk ratio is 0.989, with a 95% confidence interval from 0.769 to 1.273. These are simple unadjusted calculations from the posted group summaries. The sponsor’s risk-ratio method is identified as Cochran-Mantel-Haenszel, so the recalculation does not reproduce that method. The record does not specify the method for the sponsor’s treatment difference.

The two sets of results tell a similar broad story of estimates near no difference with intervals that include no difference, but their numerical estimates are not identical. The discrepancy flag is false. The sponsor’s own analysis therefore does not need to be displaced by the recalculation; the recalculated results serve as a transparent, unadjusted comparison rather than a substitute for the sponsor’s analysis.

15. Multiplicity, Missing Data and Analysis Populations

The primary analysis population is defined as randomized participants who received at least one dose of investigational product. This full analysis set is a clear inclusion rule, but it is not identical to an analysis of every randomized participant regardless of treatment receipt. The registry record does not report the number of randomized participants who did not receive a dose, if any, or give reasons for exclusion. It also does not describe further exclusions or the handling of participants with missing endpoint information.

The endpoint description supplies an on-treatment censoring rule: participants were censored at the last dose plus 3 months or at the end of study, whichever was earlier. That rule clarifies the evaluation window, but other missing-data details are not reported in the registry record. In particular, the record does not describe imputation, assumptions about outcomes after censoring, or sensitivity analyses addressing missingness. No additional conclusions about the amount or pattern of missing data can be drawn from the information reported.

The registry lists one primary endpoint and several secondary outcomes, but a multiplicity strategy is not reported in the registry record. It is therefore not possible to determine whether secondary tests were adjusted, ordered in a testing hierarchy, or intended to support confirmatory claims. Unadjusted testing across several outcomes can increase the chance of a false-positive finding; this is a general statistical concern, not a claim that such a finding occurred in this trial.

The original sample-size justification and trial-specific design assumptions are not reported in the registry record. The record also does not report whether interim analyses were planned or performed, whether a stopping rule was used, or the full prespecified statistical analysis plan. These omissions limit assessment of how the posted analysis relates to the original protocol. They do not alter the reported estimates, but they leave aspects of the study’s planned inferential framework unclear.

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 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: acute kidney injury (9.0%), anaemia (7.7%), cardiac failure congestive (7.4%), pneumonia (4.8%), end stage renal disease (3.2%).

The registry reports serious adverse events affecting 190 participants in the hemoglobin-based titration group and 175 in the fixed-dose group; each group had 377 participants at risk. It reports other adverse events affecting 292 and 300 participants, respectively. Deaths are listed as 38 in each group. These are descriptive counts, and the record does not provide a comparative statistical analysis of these safety outcomes in the information available for this summary.

The serious adverse event terms listed most frequently include acute kidney injury at 9.0%, anaemia at 7.7%, congestive cardiac failure at 7.4%, pneumonia at 4.8%, end stage renal disease at 3.2%, and cardiac failure at 2.9%. The registry listing does not identify these percentages by treatment group in the available information, so they should not be assigned to either arm. Serious adverse events and other adverse events are distinct summaries, and their counts should not be interpreted as counts of unique event types.

Safety counts do not by themselves establish whether a treatment strategy caused an event or whether groups differ beyond chance. The registry record does not supply the additional context needed for a fuller comparative safety assessment, such as exposure-adjusted rates or an analysis of between-group uncertainty. These figures describe what was recorded, not a clinical recommendation.

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

The primary endpoint records the proportion of participants who received at least one red blood cell transfusion during the defined on-treatment evaluation period. The observed percentages, 24.4% and 24.14%, are close, and the recalculated difference is near zero. The confidence interval nevertheless spans effects in either direction, so the result is not precise enough to establish that the underlying proportions are identical or that any difference is negligible.

A non-significant result is not proof of equivalence. The recalculated p-value is 0.932, but a p-value does not answer whether the strategies satisfy an equivalence or non-inferiority criterion. Such a conclusion requires a prespecified margin and an appropriate analysis. The registry record does not report such a margin. The result therefore supports a cautious description of similar observed event proportions, not a claim that the strategies are interchangeable.

The finding is also specific to the primary outcome definition and population. It does not directly describe the total number of transfused units, time to first transfusion, long-term outcomes beyond the reported follow-up, or outcomes among people outside the analysis population. The study concerns participants with anemia in chronic kidney disease who were not on dialysis, and the posted primary analysis includes randomized participants who received at least one dose of investigational product. Generalizing beyond that setting requires evidence not contained in these results.

Finally, the endpoint’s censoring rule means the estimate concerns events within its stated evaluation period, not every possible event after treatment ends. The registry results do not establish whether either dosing strategy changes broader clinical outcomes, nor do the statistical comparisons alone determine the balance of benefits and harms. The appropriate interpretation is confined to the posted estimates, their uncertainty, and the study’s stated design and analysis population.

18. Why This Trial Matters Statistically

This trial illustrates why a treatment comparison should be read through both its point estimate and its uncertainty. The group percentages are close, and the recalculated risk difference is near zero, but the confidence interval remains broad enough to include effects in either direction. Reporting only the point estimate or the p-value would obscure that uncertainty.

It also illustrates the distinction between a binary endpoint and related measures. Receipt of any transfusion is not the same question as the number of units transfused or time to the first transfusion. Those outcomes can provide complementary information, but they are not interchangeable. Their numerical results are not reported in the registry record, making it important to distinguish listed outcome names from posted evidence.

The comparison further shows why analysis methods matter. The sponsor reports a Cochran-Mantel-Haenszel risk ratio, while the simple recalculation is unadjusted. Both point to estimates near no difference, but method choices affect the exact estimate and interval. Transparent reporting of the analysis population, censoring rule, adjustment factors, missing-data handling, and multiplicity strategy helps readers understand what a result does and does not estimate.

Finally, planning illustrations based on an observed effect are not the same as the trial’s original design rationale or a measure of its realized evidential strength. When the observed effect is small, planning calculations can imply very large future sample sizes. This is a consequence of the assumed effect and statistical design, not a judgment about clinical value. The distinction helps prevent post hoc planning figures from being mistaken for trial design details or evidence that the completed study was adequately or inadequately planned.

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.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

The registry record leaves several trial-specific details unresolved. The brief summary describes double blinding, while the registry classification says triple masking; the record does not explain the difference or identify the masked roles. The fixed-dose arm description is truncated after its reference to placebo, limiting what can be stated about the exception for hemoglobin greater than 12.0 g/dL. The precise dose levels and full dose-adjustment rules are not reported in the registry record.

The primary result uses an on-treatment endpoint and censors participants according to the last-dose-plus-3-months or end-of-study rule. The record does not describe how missing endpoint data were handled, how many participants were censored, or whether sensitivity analyses assessed the impact of censoring. The full analysis set requires at least one dose, but the number and characteristics of any randomized participants outside that set are not reported.

The sponsor’s reported risk-ratio analysis is identified as Cochran-Mantel-Haenszel, but the stratification details are not reported in the registry record. The method for the reported treatment difference is also not specified. The original sample-size justification, interim-analysis plans, multiplicity handling, and a complete statistical analysis plan are not reported. These gaps limit independent assessment of all planned analyses and the relationship between primary and secondary testing.

The numerical secondary information available for this summary does not include results for mean transfused units, time to first transfusion, or cumulative darbepoetin alfa dose. Safety counts are descriptive, and the available serious-event term percentages are not assigned to treatment groups. These limitations narrow interpretation to the posted primary comparison and the safety summaries that are explicitly reported.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Strategies Using Darbepoetin Alfa to Avoid Transfusions in Chronic Kidney Disease — NCT01652872.
• Registry record last updated 2022-09-21; status last verified 2022-09.
• Results first posted 2018-11-08.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

The registry describes a completed phase 3, multicenter, randomized, parallel-group study of hemoglobin-based titration versus fixed-dose darbepoetin alfa in participants with anemia in chronic kidney disease who were not on dialysis. The study lists enrollment of 756 and reports 377 participants in each primary analysis group. The primary outcome was receipt of at least one red blood cell transfusion during the on-treatment evaluation period.

Observed transfusion percentages were 24.4% with hemoglobin-based titration and 24.14% with fixed dose. The recalculated unadjusted risk difference was -0.003, with a 95% confidence interval from -0.064 to 0.059 and p = 0.932. The sponsor-reported treatment difference and risk ratio also had confidence intervals including their respective no-difference values. These results describe similar observed proportions but do not establish equivalence. The registry record does not report several design and analysis details, including the original sample-size justification, multiplicity handling, and additional missing-data methods.