Genomics in Michigan Impacting Observation or Radiation: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Genomics in Michigan Impacting Observation or Radiation (NCT02783950), a randomized na study. The primary outcome is Number of Participants That Receive Adjuvant Therapy (Radiation and/or Hormone Therapy).

2. Clinical Question

The trial, Genomics in Michigan Impacting Observation or Radiation (G-MINOR), addresses whether adding genomic classifier information to clinical risk information is associated with adjuvant-treatment decisions. The registry describes the aim as determining the impact of Decipher test results compared with clinical factors alone. The primary endpoint is a treatment count, not a measure of recurrence or survival: it records participants who received adjuvant therapy within the stated timeframe and before biochemical recurrence.

The clinical question is therefore about decision-making in a defined postoperative setting. The posted results compare 19 participants in the GC arm with 12 in the usual-care-based arm for this endpoint. Those counts alone do not establish why a treatment decision was made or whether the difference reflects the classifier, other clinical considerations, or variation in care. The results also do not answer whether one strategy improves health outcomes. Secondary outcomes listed in the registry include time to adjuvant treatment, salvage treatment, biochemical recurrence, metastatic disease, and patient-reported outcomes; five secondary outcomes are posted.

3. Trial Design

The registry identifies G-MINOR as a randomized, parallel-group trial with no masking. The record lists an enrollment of 356 and a status of completed. The study began on 2017-01-17, and primary completion is recorded as 2020-02-01. The sponsor is the University of Michigan Rogel Cancer Center. The listed condition is prostate cancer.

Participants were assigned to a GC (Decipher) arm or a usual-care-based (UC) arm. In the GC period, both patients and treating physicians were to receive Decipher classifier and CAPRA-S scores following prostatectomy. In the UC period, only CAPRA-S results were provided. The registry describes randomization, but details about the allocation sequence, concealment, or how the period wording relates to assignment are not reported in the registry record. The protocol’s original sample-size assumptions are also not reported in the registry record.

The primary endpoint counts participants receiving radiation and/or hormone therapy defined as adjuvant treatment. The definition requires that treatment precede biochemical recurrence, described as PSA at least 0.2 ng/ml, and occur within 18 months of radical prostatectomy. The endpoint population includes all patients followed for at least 18 months or with an event before 18 months. The posted arm counts for this outcome are 175 in the GC arm and 165 in the UC arm. These are the outcome-specific counts; the reason they differ from the overall enrollment is not reported in the registry record.

Secondary outcomes concern treatment timing, recurrence, metastatic disease, and patient-reported outcomes. Five secondary outcomes are posted. The registry lists six outcome measures overall, but details for any additional measure are not reported in the registry record. The phase is listed as not applicable.

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

Analysis population for the primary outcome, as defined in the registry: Includes all patients who were followed for at least 18 months or had an event prior to 18 months

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 Number of Participants That Receive Adjuvant Therapy (Radiation and/or Hormone Therapy), measured over within 18 months of radical prostatectomy.

The primary endpoint is the number of participants receiving adjuvant therapy, defined as radiation and/or hormone therapy, within 18 months of radical prostatectomy and before biochemical recurrence. The registry defines biochemical recurrence using a PSA threshold of at least 0.2 ng/ml. The endpoint therefore captures whether a participant received treatment meeting both the timing and recurrence-related conditions, rather than all treatment given at any point after surgery.

A treatment-decision endpoint is relevant to this trial because its stated aim is to assess whether Decipher results affect adjuvant-treatment decisions. Counting participants who received adjuvant therapy provides a direct summary of how often the specified treatment decision occurred in each arm. It does not describe the reasons for individual decisions, the intensity or duration of treatment, or whether treatment was beneficial.

The registry specifies that the endpoint population includes patients followed for at least 18 months or who had an event before 18 months. This definition addresses the endpoint’s observation window by including participants with an earlier event as well as those followed through the full period. The posted counts are 19 of 175 in the GC arm and 12 of 165 in the UC arm. The registry does not report further details on how incomplete follow-up without an event was handled, beyond the stated population definition.

7. Results Posted in the Registry

• GC (Decipher) Arm: 10.9% (19/175) versus 7.3% (12/165) on control; risk difference 3.6 percentage points (95% CI -2.5 to 9.7), risk ratio 1.49 (0.75–2.98); unadjusted two-proportion z-test p = 0.251.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary outcome is binary at the participant level: each person either met the definition of receiving adjuvant therapy within the stated window and before biochemical recurrence, or did not. For a binary endpoint, an arm’s event count is interpreted together with the number of participants assessed. A difference in counts alone is not a fair comparison when the arm sizes differ, so the recalculation compares event risks and expresses the contrast as a risk difference.

What does a risk difference represent?

A risk difference subtracts the event risk in one arm from the event risk in the other, using the specified comparison direction. A value above zero means the estimated risk is higher in the first arm under that direction; a value below zero means it is lower. Zero represents no difference in risk. The posted recalculated estimate is positive, but its confidence interval includes zero. The estimated contrast is therefore not precise enough to rule out no difference or a difference in the opposite direction.

Other measures, such as a risk ratio or odds ratio, express the comparison on relative rather than absolute scales. Those measures can be useful, but their interpretation differs from a risk difference. The primary result is most directly understood through the event counts and the absolute contrast. No relative-effect estimate is needed to understand the core conclusion about uncertainty.

What does the chi-squared test assess?

The registry reports a chi-squared comparison with p = 0.27. In general, a chi-squared test for a binary outcome evaluates whether the distribution of event and non-event counts is compatible with the same event probability in the compared groups, under the test’s assumptions. It gives a measure of evidence against that no-difference model, not an estimate of how large or important an effect is. The p-value must be read alongside the event counts and an effect estimate with its interval.

The unadjusted recalculation reports p = 0.251. It is based on the posted summary counts and is not an adjustment for other factors. A test result can vary somewhat with the analysis method, even when the underlying counts are the same. The registry’s analysis and the recalculation should therefore be kept distinct: the former is the sponsor-reported chi-squared result, while the latter is an unadjusted reconstruction from the summary statistics. Neither p-value is a measure of clinical importance, and neither establishes that an effect is absent.

Why does the confidence interval matter?

A confidence interval expresses statistical uncertainty around an estimated effect under the model and method used to construct it. In repeated use of a method, intervals produced in this way have a coverage interpretation; for an individual trial, the interval is best read as a range of effects compatible with the data and assumptions. Here, the interval includes zero, so the observed data do not distinguish clearly between no difference and nonzero differences. The range is also relevant to precision: a wider interval leaves more uncertainty about the effect’s magnitude.

Interval interpretation depends on the outcome definition and the analytic method. The recalculated interval is unadjusted and based on summary counts. It does not incorporate unreported covariates, alternative outcome definitions, or details of follow-up that are not available in the registry record. It should not be mistaken for a result from a model that adjusts for prognostic factors.

What can the event counts tell us?

The observed counts describe the participants meeting the endpoint in the analysis population: 19 in the GC arm and 12 in the UC arm. The denominators are 175 and 165, respectively. The counts are observations, not forecasts. They provide the basis for the estimated comparison, but do not explain the clinical decisions behind each event or account for potential differences in participant characteristics.

Over-dispersion is a general concern when data vary more than a simple model expects. It is especially relevant in some count outcomes, clustered data, or repeated measurements. This endpoint is a single binary status per participant, and the registry describes a chi-squared comparison. The record does not report an over-dispersion assessment or a model requiring such an adjustment. It would therefore be inappropriate to claim that over-dispersion was assessed or found in this analysis.

What does randomization contribute?

In general, random assignment is intended to make comparison groups similar on average with respect to both measured and unmeasured characteristics, reducing confounding in expectation. It does not guarantee that groups will be identical in a particular trial, especially for factors not reported in the summary. The registry identifies this study as randomized and parallel-group, but does not report the allocation sequence, concealment details, or a covariate-adjusted analysis for this endpoint. No stronger claim about those methods is warranted from the registry record.

Overall, the methods support a descriptive comparison of event frequency and an estimate of the unadjusted contrast. Interpretation should give weight to the uncertainty interval, the modest event counts, and the boundary between treatment-decision outcomes and clinical outcomes.

10. Confidence Intervals and Precision

The recalculated risk difference is positive, but the confidence interval includes zero. That means the observed data are compatible with no difference and with nonzero differences in either direction, under the assumptions used for the calculation. The interval is therefore central to interpretation: the point estimate alone would give an incomplete picture of how uncertain the comparison is.

The limits are not repeated because the registry’s recalculated limits are recorded with more than three decimal places. At the level of detail that can be stated, the important features are that the interval crosses zero and spans effects on both sides of no difference. This does not mean every value in the interval is equally plausible, and it does not account for uncertainties outside the calculation, such as unreported analytic decisions or missing-data handling.

Precision is shaped by the number of participants and the amount of outcome information. The analysis includes 175 participants in the GC arm and 165 in the UC arm, with 19 and 12 qualifying events, respectively. With relatively few events, changing the classification of a small number of participants could affect the estimated contrast. The interval communicates this sampling uncertainty more directly than a binary significant/not-significant label.

The interval is not a guarantee about the true effect, nor does it measure clinical importance. It is an uncertainty summary tied to the stated endpoint, observed data, and method. The registry’s reported chi-squared test supplies a separate hypothesis-test result; it does not replace interval-based assessment of precision.

11. 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 effect, not the trial’s original design assumptions. For this binary endpoint, the figures are participants per arm, not total events. The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The calculations consider effects equal to 100%, 75%, and 50% of the observed effect.

For planning around 100% of the observed effect, the illustration gives 1,006 participants per arm for 80% power and 1,347 participants per arm for 90% power. For 75% of the observed effect, it gives 1,710 participants per arm for 80% power and 2,288 participants per arm for 90% power. For 50% of the observed effect, it gives 3,665 participants per arm for 80% power and 4,906 participants per arm for 90% power.

In plain terms, 80% power describes a design that would detect the specified effect in 80% of repeated trials under the planning assumptions if that effect were the true one. The 90% column describes the corresponding target for detecting it in 90% of repeated trials. These are planning targets, not guarantees for an individual study. The figures rise as the assumed effect becomes smaller: a smaller difference is harder to distinguish from random variation and requires more participants under the same assumptions.

The registry’s original sample-size rationale and design assumptions are not reported in the registry record. These illustrations are not observed power; they are hypothetical planning calculations based on the observed effect and should not be used to characterize the trial’s actual design adequacy.

12. 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 = 0.073; treatment proportion p₁ = 0.109; average p̄ = 0.091.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.4060 = 0.7958.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4052 = 0.3411.
4. n = (0.7958 + 0.3411)² / (0.0358)² = 1,006.0, rounded up to 1,006 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 <- 0.0727272727272727                          # control proportion
p1 <- 0.108571428571429                          # 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(2783950)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 1,006 (80% power), 1,347 (90% power)
 75% of observed effect: n per arm = 1,710 (80% power), 2,288 (90% power)
 50% of observed effect: n per arm = 3,665 (80% power), 4,906 (90% power)
power.prop.test: 1006 
Simulated power at n = 1,006 per arm: 0.805 (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.

13. Analyses Reported by the Sponsor

The registry reports the sponsor’s primary comparison as a chi-squared analysis with p = 0.27. The unadjusted recalculation from the posted event counts gives p = 0.251 and a positive estimated risk difference whose confidence interval includes zero. The recalculation is a simple reconstruction from summary statistics and is not an adjusted analysis.

The two p-values are close, but they are not identical. They arise from separately reported analyses and should not be blended into a new result. Both indicate that the posted comparison does not provide a clear statistical distinction between the arms under the respective test calculations. The sponsor’s reported analysis remains the trial’s own analysis; the recalculation is useful as a transparent check based on the posted counts, not as a substitute for any fuller analysis.

The registry does not report additional details about adjustment, analysis populations beyond the endpoint definition, or missing-data procedures that would explain further analytic choices. No reason for the small numerical difference between the p-values is established in the registry record.

14. Multiplicity, Missing Data and Analysis Populations

The registry lists multiple outcomes: one primary endpoint and secondary outcomes addressing treatment timing, biochemical recurrence, metastatic disease, and patient-reported outcomes. Five secondary outcomes are posted, while the record lists six outcome measures overall. Details of any additional outcome measure are not reported in the registry record.

When a study evaluates several outcomes or several comparisons, the chance of at least one apparently unusual result can increase if each is interpreted without accounting for multiplicity. In general, multiplicity procedures can control that issue by adjusting thresholds or estimates. The registry record does not report whether multiplicity was addressed, whether any secondary outcomes were designated as exploratory, or how results across outcomes were to be interpreted. The primary endpoint should therefore be distinguished from the other listed outcomes, and no claim about multiplicity control is warranted.

The primary endpoint population is described as patients followed for at least 18 months or with an event before 18 months. That definition is available, but further information on the analysis population is not reported in the registry record. In particular, details about exclusions, deviations from random assignment, and handling of participants with incomplete follow-up who did not experience an event are not reported. The outcome-specific denominators are 175 and 165; the registry does not explain their relationship to overall enrollment.

Missing-data methods can affect estimates if outcome status is unknown for some participants. General approaches include excluding participants without observed endpoint status or using explicit assumptions or models, but the registry record does not report which approach was used beyond its stated endpoint-population definition. It is not possible to infer that missingness was absent or that a particular imputation method was applied.

The record identifies the trial as randomized, but does not report whether the primary analysis followed an intention-to-treat principle, used a per-protocol population, or applied another analysis-population rule. These omissions limit assessment of how assignment, follow-up, and missing outcome information contributed to the reported estimate.

15. Safety Results

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

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 0% reporting threshold.

The registry reports serious adverse events for 182 participants at risk in the GC arm and 174 in the UC arm, with zero affected in each arm. Other adverse events are also reported as zero among 182 participants at risk in the GC arm and 174 in the UC arm. Deaths are listed as 2 in the GC arm and 0 in the UC arm.

The safety denominators differ from the primary endpoint denominators of 175 and 165. The registry record does not explain that difference, so the two sets of counts should be read as belonging to their respective outcome populations rather than treated as interchangeable. The record does not provide serious adverse event terms, and it does not report further details about the deaths, such as cause or timing. The death counts should not be assumed to represent deaths caused by treatment.

Zero reported serious or other adverse events in these groups means none were recorded in the posted categories for the stated at-risk counts. It does not establish that no adverse events occurred outside the registry’s recorded categories or observation process. These figures are descriptive and do not by themselves establish comparative safety.

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

The primary result describes how often the registry-defined adjuvant-treatment endpoint occurred in each arm: 19 participants in the GC arm and 12 in the usual-care-based arm. The recalculated estimate points toward a higher event risk in the GC arm, but the confidence interval includes zero and the reported p-values do not establish a clear between-arm difference. The data are therefore inconclusive about the magnitude and direction of the underlying difference.

The result is specific to a decision endpoint: radiation and/or hormone therapy administered before biochemical recurrence and within 18 months of radical prostatectomy. It does not measure all treatment decisions, later treatment, recurrence itself, metastatic disease, or survival. Nor does it show whether a treatment decision was appropriate for an individual patient.

The study’s stated purpose is to assess the impact of Decipher results on adjuvant-treatment decisions compared with clinical factors alone. The posted comparison is consistent with the question of whether the genomic classifier information is associated with treatment use, but the uncertainty around the estimate is substantial. The registry record does not provide enough analysis detail to assess every possible source of bias or variation.

A difference in the frequency of adjuvant treatment would not, on its own, demonstrate that classifier-informed care improves outcomes. More treatment is not necessarily better, and less treatment is not necessarily better; that depends on clinical circumstances and outcomes not captured by this endpoint. The result should not be treated as evidence for or against a treatment strategy in an individual case.

The registry also lists secondary outcomes related to treatment timing, biochemical recurrence, metastatic disease, and patient-reported outcomes. The primary comparison does not answer those questions. Its meaning is limited to the posted treatment count and comparison, with the associated uncertainty.

17. Why This Trial Matters Statistically

This trial asks a statistical question that differs from a conventional treatment-efficacy question. Its primary endpoint is whether patients receive adjuvant therapy in a defined postoperative window, making the outcome a measure of clinical decision-making. That distinction matters because a test may influence treatment choices without the treatment count alone demonstrating a change in patient outcomes.

The comparison also illustrates why a point estimate should not be read in isolation. The GC arm had 19 qualifying events and the UC arm had 12, and the recalculated estimate is positive. Yet the confidence interval includes zero. The observed direction is not the same as a precise estimate of the underlying effect. Reporting the uncertainty prevents the raw event counts from being mistaken for a settled conclusion.

There is also a useful distinction between a sponsor-reported test and a recalculation from posted summary data. The registry’s chi-squared result is p = 0.27, while the unadjusted recalculation gives p = 0.251. Keeping these analyses separate makes clear what the registry reports and what can be reconstructed from the counts, without claiming that either number captures every possible analytic choice.

Finally, the sample-size illustrations show how planning requirements depend on the effect a future study aims to detect. Smaller target effects require more participants under the stated assumptions. Those calculations are not the trial’s original design rationale, which is not reported in the registry record. Together, these features make the trial a useful example of interpreting a decision endpoint, distinguishing estimation from testing, and treating uncertainty as part of the result.

18. Limitations

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

The primary comparison has relatively few qualifying events: 19 in the GC arm and 12 in the UC arm. That limits precision, as reflected by a confidence interval that includes zero. The posted result supports a description of the observed counts, but the estimate remains uncertain.

The endpoint captures treatment only when it precedes biochemical recurrence and occurs within 18 months of radical prostatectomy. It does not cover treatment outside that definition. The registry provides the endpoint population rule, but details on incomplete follow-up without an event are not reported in the registry record. The reason the primary outcome denominators differ from total enrollment is also not reported.

Randomization is listed, but the registry record does not report allocation concealment, the sequence-generation method, or a detailed analysis-population rule. It does not report whether missing data were imputed, how multiplicity was handled, or whether covariate adjustment was planned or used. These gaps limit a full assessment of the analysis and its susceptibility to bias.

The sponsor reports a chi-squared p-value, while the recalculation is an unadjusted comparison from posted counts. The record does not explain the small difference between those p-values or provide additional modeling detail. The primary endpoint is a treatment-decision measure rather than a direct measure of health benefit, so the result cannot establish the effect of classifier-guided decisions on recurrence, metastasis, survival, or quality of life.

Safety reporting also has limitations: serious and other adverse events are recorded as zero, while deaths are listed separately, with no cause or timing reported. The safety denominators differ from the primary-outcome denominators, and the reason is not explained. These points constrain interpretation of the safety counts and do not support a broad comparative safety conclusion.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Genomics in Michigan Impacting Observation or Radiation — NCT02783950.
• Registry record last updated 2024-09-26; status last verified 2024-09.
• Results first posted 2021-02-25.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

G-MINOR is a completed, randomized, parallel-group trial with no masking, sponsored by the University of Michigan Rogel Cancer Center. It enrolled 356 participants and evaluated whether Decipher classifier results affected adjuvant-treatment decisions among high-risk patients after radical prostatectomy.

The primary endpoint was receipt of radiation and/or hormone therapy before biochemical recurrence and within 18 months of surgery. The posted counts were 19 of 175 in the GC arm and 12 of 165 in the usual-care-based arm. The sponsor reports a chi-squared p-value of 0.27; the unadjusted recalculation gives p = 0.251, with a confidence interval for the risk difference that includes zero.

The comparison is uncertain and concerns treatment use, not clinical benefit. Further details on missing-data procedures, multiplicity, original sample-size assumptions, and several analysis choices are not reported in the registry record.