Chemotherapy Administered Every 2 Weeks With or Without Pegfilgrastim in Subjects With Advanced or Metastatic Colon Cancer: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Chemotherapy Administered Every 2 Weeks With or Without Pegfilgrastim in Subjects With Advanced or Metastatic Colon Cancer (NCT00094809), a randomized phase 2 study. The primary outcome is Grade 3 or 4 Neutropenia.

2. Clinical Question

The primary question concerns a specific laboratory-defined safety outcome during an early period of chemotherapy. Neutropenia was defined in the registry as an absolute neutrophil count (ANC) < 1 x 10^9/L. The study also recorded outcomes related to treatment delays or reductions, febrile neutropenia, hospitalization, tumor response, disease progression and survival.

The comparison is between the assigned study-drug groups, not between chemotherapy regimens. The registry summary says pegfilgrastim was evaluated after three regimens, but regimen-specific outcome estimates are not reported in the registry record. The posted primary result therefore describes the comparison across the primary analysis set and does not establish whether the estimate was similar for each chemotherapy regimen.

3. Trial Design

This was a Phase 2, randomized, double-blind, parallel-group trial sponsored by Amgen. The registry lists an enrollment of 252 participants and a completed study. The study began on 2003-02-01, and primary completion was recorded on 2006-05-19. The two interventions were pegfilgrastim and placebo, each described as a 6 mg injection.

Participants had locally advanced or metastatic colorectal cancer and received first- or second-line treatment with one of FOIL, FOLFOX or FOLFIRI, according to the registry summary. The trial evaluated pegfilgrastim administered after chemotherapy, with the registry describing an 11-day interval before the next chemotherapy cycle. The record characterizes that interval as the reason the study was investigational.

Randomization is intended to make treatment groups comparable on average, while double masking is intended to reduce the influence of treatment knowledge on participant care and outcome assessment. These are general design principles; the methods used to generate the allocation sequence, conceal assignments, and maintain masking are not reported in the registry record. The allocation ratio and any stratification factors are also not reported in the registry record.

The primary outcome was assessed during the first four cycles of treatment (8 weeks). The primary analysis set included participants who received study drug and signed informed consent before any invasive procedures. The registry lists 123 participants in the pegfilgrastim group and 118 in the placebo group for the primary outcome. The reason these outcome counts differ from the overall enrollment is not reported in the registry record. Details of the trial's original sample-size calculation and its planned statistical analysis are not reported in the registry record.

4. Participant Flow and Accounting

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

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Primary Analysis Set, composed of all participants who received study drug and who signed an informed consent before any invasive procedures

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 Grade 3 or 4 Neutropenia, measured over First 4 cycles of treatment (8 weeks).

The primary endpoint counted participants with grade 3 or 4 neutropenia in any of the first four treatment cycles (8 weeks). The registry defines the condition as an absolute neutrophil count (ANC) < 1 x 10^9/L. It is a binary outcome: each participant either met the definition during the specified period or did not. The posted arm results are counts of participants with an event, rather than counts of individual episodes.

Neutropenia is relevant to chemotherapy because it is a blood-count outcome that can be associated with infection risk and changes to treatment delivery. The registry also includes dose delay or reduction due to neutropenia and febrile neutropenia among the recorded outcomes. Those are related but distinct measures: the primary endpoint is based on the ANC threshold, not on whether a dose was changed or fever occurred.

Using a prespecified threshold and a defined observation period makes the outcome interpretable as a comparison of event occurrence during early treatment. It does not describe the duration or severity beyond the grade definition, later cycles, or individual participants' clinical circumstances. The laboratory measurement schedule, rules for handling missing ANC assessments, and details of any independent endpoint review are not reported in the registry record.

7. Results Posted in the Registry

• Pegfilgrastim (Neulasta): 13.0% (16/123) versus 43.2% (51/118) on control; risk difference -30.2 percentage points (95% CI -40.9 to -19.5), risk ratio 0.30 (0.18–0.50); unadjusted two-proportion 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.

Dose Delay or Reduction Due to Neutropenia

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Pegfilgrastim (Neulasta): 4.1% (5/123) versus 22.0% (26/118) on control; risk difference -18.0 percentage points (95% CI -26.2 to -9.7), risk ratio 0.18 (0.07–0.46); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Pegfilgrastim (Neulasta) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Dose Delay or Reduction for Any Reason

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Pegfilgrastim (Neulasta): 33.3% (41/123) versus 44.9% (53/118) on control; risk difference -11.6 percentage points (95% CI -23.8 to 0.7), risk ratio 0.74 (0.54–1.02); unadjusted two-proportion z-test p = 0.065.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Pegfilgrastim (Neulasta) and the control. The interval gives the range of effects that remain compatible with the data.

Febrile Neutropenia

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Pegfilgrastim (Neulasta): 2.4% (3/123) versus 8.5% (10/118) on control; risk difference -6.0 percentage points (95% CI -11.8 to -0.3), risk ratio 0.29 (0.08–1.02); unadjusted two-proportion z-test p = 0.038.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Pegfilgrastim (Neulasta) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Across the secondary comparisons with detailed results in the registry record, the point estimates generally favor fewer events in the pegfilgrastim group for outcomes related to neutropenia and dose modification. The results do not form a single uniform pattern across all secondary outcomes: the comparison for dose delay or reduction for any reason is less conclusive than the primary comparison, and the estimates for febrile neutropenia are based on relatively few recorded events. The posted results also include outcomes with very different meanings, so they should not be combined into one overall claim.

These secondary outcomes relate to the primary result because dose changes due to neutropenia and febrile neutropenia are clinically and conceptually connected to low neutrophil counts. They are not equivalent to the ANC-defined primary endpoint. A lower count for one outcome does not establish the same effect for another, and the registry record does not provide analyses by chemotherapy regimen that could clarify whether the pattern varied across FOIL, FOLFOX and FOLFIRI.

The registry record lists other outcomes, including hospitalization, objective tumor response, progression-free survival, survival and antibiotic use due to febrile neutropenia, but detailed results for these are not reported in the registry record. The broad list of outcomes should not be mistaken for evidence that each outcome demonstrated a particular pattern.

Unadjusted secondary results carry less weight because multiple outcomes can be tested and the registry does not report a multiplicity adjustment or testing hierarchy. General explanation: when many separate tests are considered, some may appear notable by chance even if there is no underlying difference for those outcomes. Secondary estimates and intervals can still be informative, especially for understanding consistency and uncertainty, but they do not have the same interpretive standing as the designated primary comparison.

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

• Dose Delay or Reduction Due to Neutropenia
• Dose Delay or Reduction for Any Reason
• Febrile Neutropenia
• Hospitalization Due to a Neutropenia-Related Event
• Progression-Free Survival
• Objective Tumor Response
• Survival
• Antibiotic Use Due to Febrile Neutropenia

9. Statistical Interpretation

10. Statistical Methods Explained

What does the primary comparison estimate?

The primary endpoint is binary, because the posted result classifies each participant according to whether grade 3 or 4 neutropenia occurred during the first four cycles. A treatment comparison can be expressed in several ways. The sponsor reported an odds ratio, while the recalculation uses a risk difference. General explanation: a risk difference is an absolute contrast between the event proportions in two groups; an odds ratio compares the odds of an event in one group with the odds in the other. The same data can produce different numerical values on these scales, so the scales should not be read as though they were identical.

The sponsor's primary analysis is reported as Mantel-Haenszel, with an odds ratio of 0.19 and a 95% confidence interval from 0.10 to 0.37. The registry does not describe which strata, if any, were used for this analysis. The registry's methods for covariate adjustment, missing outcome handling, and sensitivity analyses are not reported in the registry record. The unadjusted recalculation is based on the posted summary counts and is not a replacement for the sponsor's analysis.

What does a confidence interval communicate?

General explanation: a confidence interval describes the statistical uncertainty around an estimate under the assumptions of the method used. It gives a range of values reasonably compatible with the observed data and model. It does not mean that the true value has a specified probability of lying in that particular interval, and it does not capture every source of uncertainty, such as bias from missing data or limitations in how participants were selected.

For an odds ratio, the null value is 1, which represents equal odds between groups. For a risk difference, the null value is 0, which represents no absolute difference. The primary sponsor-reported interval lies below the odds-ratio null value. The recalculated risk-difference interval is a separate estimate on a different scale. The p-value tests a null hypothesis according to the method used; it is not a measure of effect size or the probability that the null hypothesis is true.

How should the secondary analyses be understood?

The registry reports Mantel-Haenszel analyses for the listed secondary comparisons, but the reported effect measures vary: some are treatment differences and others are odds ratios. A treatment difference is an absolute contrast, while an odds ratio is relative on the odds scale. Interpretation should therefore follow the measure and interval attached to each outcome, rather than comparing the raw estimates across different scales.

General explanation: when several outcomes are examined, the chance of obtaining at least one apparently unusual result can increase if each is tested separately without adjustment. The registry record does not report a multiplicity strategy, a prespecified hierarchy of secondary endpoints, or whether any outcomes were designated as confirmatory. Secondary findings should consequently be treated as exploratory or supportive unless the registry record establishes a stronger inferential plan.

The recorded outcomes also differ in what they measure. A dose modification is a treatment-delivery event, febrile neutropenia is a clinical event, and progression-free survival or survival are time-to-event outcomes. A finding for one does not automatically establish a finding for another. The registry record lists outcomes including hospitalization, objective tumor response, progression-free survival, survival and antibiotic use, but detailed results for all of these are not reported in the registry record.

What can the analysis population tell us?

The primary analysis population is defined in the registry as participants who received study drug and signed informed consent before any invasive procedures. This definition helps identify who contributed to the posted primary analysis, but it is not enough to determine whether the analysis followed an intention-to-treat principle. The registry does not report how participants who were randomized but did not receive study drug were handled, or how missing outcome measurements were treated. Those details matter because exclusions or missing measurements can affect how representative the analyzed groups are of everyone randomized.

General explanation: randomization supports causal interpretation when group assignment is preserved in the analysis and outcome measurement is sufficiently complete and comparable. A registry summary alone cannot verify those conditions. The reported treatment contrast should therefore be read as an estimate from the stated primary analysis set, with the analysis details and completeness of follow-up left uncertain where the record is silent.

11. Confidence Intervals and Precision

The primary sponsor-reported estimate is an odds ratio of 0.19, with a 95% confidence interval from 0.10 to 0.37. Because the entire interval is below the null odds ratio of 1, the interval is consistent with lower odds of the recorded primary event in the pegfilgrastim group under this analysis. The interval also shows that the estimate is not a single known value: a range of effect sizes remains compatible with the data and method.

General explanation: a narrower confidence interval indicates greater statistical precision on the scale being used, while a wider interval indicates more uncertainty. Precision depends in part on the amount of information available, including the number of participants and events, but it is not the same as the importance of an effect. A confidence interval also does not account for every potential source of bias or uncertainty in trial conduct.

The posted primary event counts are 16 of 123 in the pegfilgrastim group and 51 of 118 in the placebo group. They give context for the estimate, but do not remove uncertainty about the size of the difference in other settings. The reported odds-ratio interval is not an interval for an absolute risk difference; readers should keep the measure and its scale in view when interpreting the estimate.

Secondary estimates are less uniform in their precision. For example, the posted analysis for dose delay or reduction for any reason has a reported 95% interval extending from -23.7 to 0.5 for the treatment difference. The registry's febrile-neutropenia analysis reports an odds ratio of 0.27 with a 95% interval from 0.07 to 1.00. These intervals illustrate why a direction of the point estimate alone is insufficient: an interval may include values compatible with little or no difference. The multiplicity and population limitations described elsewhere also remain relevant to the interpretation of precision.

12. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The planning figures are illustrations based on the observed effect, not the trial's original design calculation. For these binary outcomes, the figures refer to participants per arm, not total events. The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. Each planning row uses a stated fraction of the observed effect as the effect to detect. The original trial's own sample-size assumptions are not reported in the registry record.

The 80% power column represents the planned number of participants per arm under which the calculation would have an 80% chance of detecting the specified effect at the stated significance level, if the planning assumptions and effect were correct. The 90% power column uses a higher chance of detection and therefore generally calls for more participants per arm under the same assumptions. These are planning concepts, not guarantees about what a future study will observe.

Rows that plan for 75% or 50% of the observed effect use smaller target effects than the row based on the full observed effect. Smaller effects are harder to distinguish from random variation, so they require more participants. This is why the planning counts rise as the assumed effect becomes more modest. The values are illustrations, not a claim that the trial was designed around the observed effect, and they do not establish the probability that the trial's result is correct.

This is not observed power. Observed power is not a useful substitute for reading the estimate and its confidence interval after a study is complete. The planning values instead show how sample-size requirements would change under specified assumptions. They should not be treated as the trial's actual sample-size justification, because that justification is 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, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.432; treatment proportion p₁ = 0.130; average p̄ = 0.281.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6358 = 1.2461.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5988 = 0.5040.
4. n = (1.2461 + 0.5040)² / (-0.3021)² = 33.6, rounded up to 34 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 <- 0.432203389830508                          # control proportion
p1 <- 0.130081300813008                          # 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(94809)
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 = 34 (80% power), 45 (90% power)
 75% of observed effect: n per arm = 66 (80% power), 87 (90% power)
 50% of observed effect: n per arm = 157 (80% power), 210 (90% power)
power.prop.test: 33.6 
Simulated power at n = 34 per arm: 0.827 (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's primary analysis is reported as a Mantel-Haenszel odds ratio of 0.19, with a 95% confidence interval from 0.10 to 0.37 and p < 0.001. The recalculation uses the posted group counts to express the comparison as an unadjusted risk difference. It is a simple summary-statistic calculation on a different effect scale, rather than an attempt to reproduce all details of the sponsor's analysis.

The two estimates answer related but not identical questions. The odds ratio compares group odds, while the risk difference compares event proportions on an absolute scale. Their numerical values should not be compared directly. The direction of the primary sponsor result is compatible with the lower event count in the pegfilgrastim group, but the sponsor's own analysis remains the principal reported inferential result.

The registry does not report enough detail to reproduce the Mantel-Haenszel analysis, including any stratification choices or other implementation details. The recalculation also cannot address any participant-level covariates or missing data. There is no reported discrepancy between the sponsor analysis and the posted summary-statistic recalculation. Differences in reported numerical values across methods or scales should therefore be understood in terms of the analysis measure and method, rather than treated as contradictory findings.

15. Multiplicity, Missing Data and Analysis Populations

The registry record does not report whether the trial's statistical plan adjusted for multiple comparisons, used a hierarchical testing sequence, or designated any secondary endpoint as confirmatory. It also does not report how the study handled interim analyses or whether any were planned or conducted. These details should not be inferred from the fact that the registry lists numerous outcomes and analyses.

General explanation: testing multiple outcomes increases the opportunity for chance findings when each result is assessed separately. A multiplicity procedure can control a prespecified error rate, but it may also affect how evidence is interpreted across outcomes. Without a reported plan, secondary p-values should be read as individual, unadjusted evidence rather than as results protected from the consequences of testing many outcomes. The primary endpoint remains the clearest stated focal comparison, while secondary findings are supportive and require caution.

The primary analysis set is described as participants who received study drug and signed informed consent before any invasive procedures. The registry does not report whether this population was defined before unblinding, how it relates to all randomized participants, or how participants with missing assessments were handled. It does not report imputation methods, rules for incomplete follow-up, or sensitivity analyses addressing missing data. The reasons for any difference between enrollment and the primary outcome group sizes are not reported in the registry record.

These omissions limit assessment of potential bias. General explanation: if missing outcome data or post-randomization exclusions differ between groups, the analyzed comparison may not fully preserve the balance created by randomization. The registry summary does not establish whether that occurred in this trial. It is therefore appropriate to describe the posted estimate as applying to the stated primary analysis set, rather than assume it represents every randomized participant under an intention-to-treat analysis.

The original statistical analysis plan, sample-size justification, and details of any interim monitoring are not reported in the registry record. Without them, it is not possible to determine from the registry whether all reported outcomes and analyses followed the original plan or whether any decisions were made after results were examined.

16. 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: dehydration (11.3%), nausea (6.0%), neutropenia (5.6%), diarrhoea (5.6%), febrile neutropenia (5.1%).

The serious adverse event record reports 36 affected participants among 117 at risk in the placebo group and 44 among 124 at risk in the pegfilgrastim group. These figures count participants with at least one serious adverse event in the registry's reporting, not necessarily the total number of separate events. The record also lists dehydration, nausea, neutropenia, diarrhoea, febrile neutropenia and vomiting among the most frequently reported serious-event terms, with percentages of 11.3%, 6.0%, 5.6%, 5.6%, 5.1% and 5.1%, respectively.

The listed term percentages are not assigned to a particular arm in the registry record, so they should not be interpreted as arm-specific comparisons. Counts alone do not establish whether an event was caused by the study drug, how severe or prolonged it was, or when it occurred. The registry does not report deaths in the serious adverse event fields, and the methods for collecting or adjudicating adverse events are not reported in the registry record. The serious-event figures are descriptive safety information and should be considered separately from the primary neutropenia endpoint.

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

The posted primary results show fewer participants meeting the registry's grade 3 or 4 neutropenia definition in the pegfilgrastim group than in the placebo group during the first four treatment cycles (8 weeks). The sponsor's reported odds ratio and confidence interval are consistent with lower estimated odds of this event in the pegfilgrastim group in the primary analysis set. This is a description of the trial's observed comparison, not a general conclusion about every patient or chemotherapy setting.

The result does not establish that pegfilgrastim has the same effect with each of the three chemotherapy regimens. Regimen-specific results are not reported in the registry record. It also does not answer questions about longer-term outcomes, because the primary endpoint covered the early treatment period and detailed results for progression-free survival, survival and objective tumor response are not reported in the registry record.

The result does not, by itself, determine the balance of all potential benefits and harms. Serious adverse events were reported in both groups, and the registry's summary does not provide enough information to assess causality, timing, or individual event profiles by treatment. The primary endpoint is an ANC-defined event, whereas dose modifications and febrile neutropenia are separate outcomes. Findings for these outcomes should not be treated as interchangeable.

Finally, the statistical result does not remove uncertainties about missing data, the exact analysis population, the original statistical plan, or multiplicity. Those details are not reported in the registry record. The confidence interval describes sampling uncertainty under its method, but does not resolve limitations in trial conduct or establish the result's applicability beyond the studied population and treatment context.

18. Why This Trial Matters Statistically

This trial illustrates why the effect measure matters in biostatistical interpretation. Its sponsor-reported primary result is an odds ratio, while a simple recalculation from the posted counts uses a risk difference. Both describe the same two-group comparison from different perspectives, but their numerical scales and clinical interpretations differ. Keeping those measures distinct avoids treating an odds ratio as though it were an absolute change in event frequency.

It also shows the value of reading an estimate alongside its confidence interval and the underlying event counts. A p-value alone does not convey the magnitude or precision of an effect. The primary sponsor-reported interval is entirely below the odds-ratio null value, whereas some secondary intervals are compatible with little or no difference. That contrast helps distinguish the strength and precision of findings without making a clinical recommendation.

The study includes multiple related outcomes, including laboratory-defined neutropenia, dose changes and febrile neutropenia, as well as more distant outcomes such as survival. These outcomes answer different questions. Their relationship does not justify treating them as one composite result, particularly when a multiplicity strategy is not reported.

Finally, the registry makes visible important limits on interpretation: the stated primary population, the early endpoint timeframe, the lack of regimen-specific estimates, and missing details about sample-size justification, missing data and analysis planning. For clinical researchers, those omissions are not minor technicalities. They define what can responsibly be concluded from a registry-level statistical summary and what remains uncertain.

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 primary endpoint applies to the first four cycles of treatment (8 weeks), not to the full course of therapy or longer-term outcomes. The registry does not report regimen-specific estimates, so the overall result cannot establish whether the comparison was consistent across FOIL, FOLFOX and FOLFIRI. It also does not describe subgroup analyses by line of treatment or other participant characteristics.

The primary outcome group sizes are 123 and 118, while the overall enrollment is 252. The reasons for the difference are not reported in the registry record. The primary analysis set is defined by receipt of study drug and consent timing, but the registry does not say how this set relates to all randomized participants or how missing outcome measurements were addressed. This restricts assessment of how closely the reported analysis preserves the randomized comparison.

The trial's original sample-size justification and full statistical analysis plan are not reported. The registry also does not report a multiplicity strategy, interim analysis details, or the handling of incomplete data. These gaps limit evaluation of whether secondary findings were prespecified and how the reported uncertainty should be interpreted across the full set of outcomes.

Finally, the serious adverse event summary does not establish causality or provide event timing and arm-specific breakdowns for the listed terms. Detailed results for several listed secondary outcomes, including progression-free survival and survival, are not reported in the registry record. The posted information therefore supports a focused interpretation of the primary comparison, not a complete assessment of all clinical outcomes or safety dimensions.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Chemotherapy Administered Every 2 Weeks With or Without Pegfilgrastim in Subjects With Advanced or Metastatic Colon Cancer — NCT00094809.
• Registry record last updated 2018-10-17; status last verified 2018-09.
• Results first posted 2011-01-06.
• 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

NCT00094809 is a completed Phase 2, randomized, double-blind, parallel-group trial sponsored by Amgen. It enrolled 252 participants with locally advanced or metastatic colorectal cancer and compared 6 mg pegfilgrastim with 6 mg placebo after chemotherapy. The registry lists FOIL, FOLFOX and FOLFIRI as the chemotherapy regimens.

The primary outcome was grade 3 or 4 neutropenia, defined as ANC < 1 x 10^9/L during the first four cycles of treatment (8 weeks). The sponsor reported a Mantel-Haenszel odds ratio of 0.19, with a 95% confidence interval from 0.10 to 0.37 and p < 0.001. Important details, including the original sample-size justification, missing-data approach and multiplicity plan, are not reported in the registry record.