Prevention of Metabolic Complications of Glucocorticoid Excess: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Prevention of Metabolic Complications of Glucocorticoid Excess (NCT01319994), a randomized phase 2, phase 3 study. The primary outcome is CT Abdomen.

2. Clinical Question

3. Trial Design

The registry describes a completed randomized, parallel-group study with metformin and placebo arms. It lists the study as Phase 2 and Phase 3, gives enrollment as 57, and records the condition as iatrogenic Cushing disease. The listed sponsor is Barts & The London NHS Trust. The start date is 2012-07 and primary completion is recorded as 2014-08.

The intervention descriptions specify metformin 850mg TDS for 12 weeks and placebo 850mg TDS for 12 weeks. The brief summary describes a prospective, randomized, double-blind, placebo-controlled study. Separately, the registry masking field says triple masking. Those descriptions are both retained in the record, without an explanation of how the masking categories relate.

The primary endpoint is expressed as a change from baseline at 3 months, and the posted arm summaries include 19 participants in the metformin group and 21 in the placebo group. These endpoint summary counts differ from the enrollment figure, but the registry record does not explain the relationship between enrollment and the analyzed endpoint populations. Safety summaries use different at-risk counts. The record does not report the original sample-size justification, detailed eligibility criteria, treatment adherence, or a participant-flow account.

The study aim in the registry summary was to investigate metformin's effect on metabolic parameters in patients receiving long-term high-dose glucocorticoids. The record includes one secondary outcome, HOMA2-IR. Although the trial is marked completed, the posted record does not list reported analyses in the secondary-outcome entry.

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: Patients were recruited into "Prevention" and "Treatment" algorithms initially. However, only the "Treatment" algorithm proved feasible for logistic reasons. Below are the results relating to patients randomized into the Treatment algorithm.

Overall Study

Reasons for not completing this period:

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.

Population: Heterogeneous but well matched treatment groups

6. Primary Endpoint

The registry lists the primary outcome as CT Abdomen, measured over 3 months minus baseline.

The primary endpoint is the change in the CT abdomen ratio for visceral/subcutaneous fat, measured as the value at 3 months minus the baseline value. It is a continuous measure, and the registry describes the reported arm values as means with standard deviations. The endpoint therefore summarizes the average change in this imaging-based measure within each treatment group.

Visceral and subcutaneous fat are distinct abdominal fat compartments. A ratio provides a relative measure of those compartments rather than a direct measure of either compartment alone. In general, a CT-based measure can quantify body composition at the imaged region, while a change score expresses how that measure differed between the two recorded time points. The registry describes the endpoint as “change in visceral/subcutaneous fat” and gives its unit as ratio.

The registry summary connects the study to metabolic complications of glucocorticoid excess, making an abdominal fat measure relevant to its stated metabolic focus. However, this endpoint is not itself a direct measurement of all metabolic complications. The posted primary result does not establish what happened to other clinical outcomes, nor does it describe whether changes persisted after the 12-week treatment period. The record does not report further details about CT acquisition, image reading, or the construction of the ratio.

7. Results Posted in the Registry

• Metformin: mean 0.08 versus -0.03 on control; difference 0.11 (95% CI -0.02 to 0.24), standardized effect d = 0.53; z-test p = 0.090.

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.

HOMA2-IR

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Metformin: mean 0.22 versus 2.35 on control; difference -2.13 (95% CI -4.14 to -0.12), standardized effect d = -0.66; z-test p = 0.038.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Metformin than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registry lists one secondary endpoint, HOMA2-IR, a continuous measure reported as change from baseline to 3 months. The direction of its posted group contrast differs from the direction of the primary CT ratio contrast. Because the outcomes measure different aspects of metabolism and use different scales, their signs cannot be compared as if they represented the same quantity. The secondary result adds a separate observation rather than resolving the uncertainty in the primary endpoint.

The registry summary describes the study's broad aim as examining metabolic parameters during long-term high-dose glucocorticoid treatment. In that context, HOMA2-IR is relevant as a distinct metabolic measure, while the CT abdomen endpoint concerns a ratio for visceral/subcutaneous fat. A pattern across these outcomes can be informative, but one measure does not substitute for another, and neither alone captures every metabolic complication discussed in the study rationale.

The secondary comparison has an unadjusted p-value, and the registry does not report a multiplicity plan, an outcome hierarchy, or detailed analyses for this entry. In general, when several outcomes are considered, an isolated result that appears statistically notable can arise more readily than when only one prespecified comparison is tested. Adjustments or a prespecified hierarchy can help control interpretation, but whether either approach was used is not reported in the registry record.

The secondary result should therefore carry less inferential weight than a clearly prespecified primary outcome with a documented analysis plan. This is not because secondary outcomes are inherently uninformative; rather, their interpretation depends on prespecification, the number of analyses undertaken, missingness, and the analysis strategy. The record lists no reported analyses in the secondary entry and does not resolve these points. It is reasonable to treat the secondary finding as supportive context for further study, not as an independent confirmation of the primary result.

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

• HOMA2-IR

9. Statistical Interpretation

10. Statistical Methods Explained

The posted outcomes are continuous measures summarized by means and standard deviations. For the primary endpoint, each arm's mean represents the average change in the CT abdomen ratio from baseline to 3 months. The standard deviation describes variation in individual changes around that arm's mean. It is not the uncertainty in the mean itself: precision of an arm mean also depends on the number of observations contributing to it.

What does the mean difference represent?

The reported mean difference compares the average change in the metformin group with the average change in the placebo group. The subtraction order is metformin minus placebo. A positive estimate means the mean change was higher in the metformin group on the outcome's recorded scale; a negative estimate means it was lower. This is an unadjusted comparison of the posted summary statistics. The registry record does not describe covariate adjustment, a model-based adjustment for baseline values, or other details of the sponsor's primary analysis.

In general, a mean difference preserves the original measurement scale, which makes it easier to relate the estimate to the measured outcome than a standardized effect. It also depends on how the outcome is defined and coded. Here, interpretation must account for the fact that the endpoint is a ratio change, and the record does not provide a clinical threshold for interpreting a particular difference.

What does the confidence interval add?

A confidence interval gives a range of values compatible with the observed data under the statistical method and its assumptions. In repeated use of the same method, intervals constructed this way would cover the fixed target parameter at the stated rate. It is not a probability statement about the specific interval containing the true value. For the primary comparison, the posted interval includes zero; the data therefore do not rule out a zero contrast at the interval's confidence level. The range also conveys how much uncertainty remains about the size and direction of the contrast.

How should the p-value be understood?

The unadjusted p-value summarizes how unusual data at least as incompatible with a no-difference model would be if that model and the test assumptions held. It is not an effect size and does not indicate clinical importance. A smaller p-value does not automatically mean a larger or more useful effect. The p-value shown for the primary outcome is explicitly unadjusted. The record does not report the precise inferential test, whether assumptions were checked, or whether any planned adjustment was part of the sponsor's analysis.

Why do standard deviations matter?

Standard deviations describe the spread of observed changes within groups. When variability is large relative to the mean difference, it is harder to estimate a between-group contrast precisely from a given amount of data. General statistical reasoning treats such variability as important when interpreting confidence intervals and planning future studies. The primary endpoint's arm standard deviations are posted, as are pooled spread and standardized-effect summaries in the recalculation. Those summaries describe the observed data; they do not establish that a future study would have the same variability or effect.

The posted recalculation is a simple unadjusted calculation based on summary statistics. Because the discrepancy flag is false, no sponsor-analysis precedence issue is indicated by the record. Still, a recalculation cannot reproduce unavailable details of an original analysis, such as the exact model, handling of missing observations, or any adjustments. Those details are not reported in the registry record.

What is the role of randomization?

In general, random allocation is intended to make treatment groups comparable on average with respect to characteristics known and unknown at assignment. It supports a between-group interpretation when allocation is implemented as intended and outcome data and analyses are handled appropriately. The registry records randomized allocation, but does not report the sequence-generation method, concealment procedures, stratification, or the analysis population. Those omissions limit assessment of how randomization was implemented and how closely the posted endpoint comparison follows the original trial plan.

The registry also identifies a parallel model, meaning participants were assigned to one of the trial arms rather than described as crossing between treatments. The brief summary calls the study double-blind, while the masking field records triple masking. In general, masking can reduce the influence of expectations on care, reporting, and outcome assessment, but the record does not identify which groups of people were masked or explain the difference in masking labels.

What can and cannot be inferred from the secondary measure?

The secondary measure, HOMA2-IR, is reported as a continuous HOMA score change from baseline to 3 months, with arm means and standard deviations. Its comparison uses the same general mean-difference interpretation but has a different scale and represents a different outcome. In general, results across outcomes can provide complementary evidence, but a result on one measure does not mechanically validate another. The registry's reported analyses list is empty for this secondary entry, and the record does not provide a detailed statistical analysis plan.

General statistical principles also distinguish an observed estimate from a prespecified confirmatory test. When multiple outcomes or comparisons are examined, the chance of at least one apparently notable result can increase unless the analysis plan accounts for multiplicity. The registry does not report whether such an adjustment or hierarchy was planned. This uncertainty is one reason to treat the secondary result more cautiously than a clearly prespecified primary test, without assuming that an unreported method was or was not used.

11. Confidence Intervals and Precision

The primary mean difference is 0.11, with a 95% confidence interval from -0.017 to 0.237. The interval crosses zero, so the result does not identify a clear direction at that confidence level. Its lower end permits a small negative difference, while its upper end permits a larger positive difference. The point estimate should therefore be read together with the interval rather than as a precise single answer.

Precision concerns how narrowly the data estimate the contrast, not whether the estimate is important in practice. A narrow interval would imply less statistical uncertainty about the mean difference; a wider interval would leave more possible values compatible with the data. The registry does not provide a threshold for a clinically meaningful change in the CT ratio, so the interval cannot be classified as excluding or including a meaningful effect on that basis.

The arm summaries report 19 participants for metformin and 21 for placebo. The record does not explain why these counts differ from the enrollment figure, or whether all randomized participants contributed to this endpoint. Missing outcome handling and the primary analysis population are not reported in the registry record. Both are relevant to how confidently the interval represents the randomized comparison.

In general, confidence intervals depend on the statistical method and its assumptions, including how variability is estimated and how observations are treated. The posted interval is available, but the registry does not document the underlying test or model in enough detail to independently assess those assumptions. The unadjusted p-value of 0.09 complements the interval but does not replace it: the interval conveys a range of plausible contrasts, while the p-value summarizes evidence relative to a no-difference model.

12. Planning a Similar Trial: Sample Size

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

The sample-size table and curve are planning illustrations based on the observed effect, not the trial's original design calculation. The listed assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each row uses a stated fraction of the observed effect as the effect to detect. The original trial's sample-size assumptions and justification are not reported in the registry record.

The columns give participants per arm for 80% power and participants per arm for 90% power. In plain terms, the 80% column represents a planning target under which a study with the stated assumptions would have an 80% chance of detecting the specified effect if that effect were the true one. The 90% column uses a higher chance of detection under the same type of assumptions. These are prospective design calculations, not descriptions of what happened in this completed trial.

Rows for smaller fractions of the observed effect require more participants per arm because a smaller difference is harder to distinguish from random variation. The table and curve show how the planning requirement changes as the target effect becomes more conservative. They should not be interpreted as evidence that the trial had a particular probability of finding an effect after its results were known. This is not observed power.

The illustration relies on the observed effect and planning assumptions that may not match the original design or a future study. In general, planning is also sensitive to expected variability, the selected outcome, analysis method, loss of outcome data, and multiplicity choices. The registry does not report the original design assumptions for these considerations. Accordingly, the listed figures are best read as scenario-based planning aids, not as a retrospective judgment about trial conduct.

13. How the Sample Size Is Derived

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

Formula

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

Worked calculation for this trial

1. Observed difference Δ = 0.110; pooled standard deviation σ = 0.206.
2. n = 2 × (1.96 + 0.842)² × 0.206² / 0.110² = 55.2, rounded up to 56 participants per arm for 80% power.

The smaller-effect rows in the table above repeat the same calculation with the effect multiplied by 0.75 and 0.5 (for ratios, applied to the logarithm of the ratio).

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
delta <- 0.11                      # observed difference in means
sigma <- 0.206333914348869                     # pooled standard deviation
n_per_arm <- function(power, frac = 1) {
  ceiling(round(2 * (z_a + qnorm(power))^2 * sigma^2 / (delta * frac)^2, 6))
}
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: n per arm = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(n_per_arm(0.80, f), big.mark = ","), format(n_per_arm(0.90, f), big.mark = ",")))

# Check against R's built-in function (t-based, so very slightly larger)
cat("power.t.test:", round(power.t.test(delta = delta, sd = sigma, power = 0.80)$n, 1), "\n")

# Simulation: exact two-sample t-test using simulated means and variances
set.seed(1319994)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 56 (80% power), 74 (90% power)
 75% of observed effect: n per arm = 99 (80% power), 132 (90% power)
 50% of observed effect: n per arm = 221 (80% power), 296 (90% power)
power.t.test: 56.2 
Simulated power at n = 56 per arm: 0.799 (20000 replicates)

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

14. Multiplicity, Missing Data and Analysis Populations

The registry record does not report whether the trial used an adjustment for multiple testing, a prespecified hierarchy of outcomes, or another multiplicity strategy. The record lists one primary endpoint and one secondary endpoint, but it does not establish whether these were the only outcomes examined or whether other comparisons were planned. The secondary entry has no reported analyses listed. Without a documented plan, the unadjusted p-values should be interpreted as nominal results rather than as evidence that a family-wise error rate or another multiplicity target was controlled.

In general, multiplicity matters when researchers examine more than one endpoint, time point, subgroup, or analytic comparison. Considering more tests increases the chance of seeing at least one small p-value even if all corresponding null hypotheses are true. A correction can reduce that risk, usually at the cost of requiring stronger evidence for an individual comparison. The correct approach depends on the planned scientific questions and analysis hierarchy; the record does not say which approach was selected.

Missing outcome data are also not described in enough detail to evaluate their effect. The registry provides endpoint-specific group counts, while the overall enrollment figure and safety at-risk counts are different. It does not report participant flow, reasons for missing measurements, imputation, or whether the primary analysis followed an intention-to-treat, per-protocol, or other population definition. These matters are not interchangeable: the number randomized, the number with an available measurement, and the number included in an analysis can differ.

In general, missingness can affect an estimate when the likelihood of having an observed outcome is related to treatment assignment or to the outcome itself. Methods that assume missing data are unrelated to unobserved values require assumptions that may not be verifiable from summary results alone. The registry does not report the approach used or provide enough information to evaluate those assumptions.

The record also does not report the full statistical analysis plan, the handling of protocol deviations, or whether baseline adjustment was planned. These omissions do not demonstrate that a particular method was inappropriate; they mean that independent assessment of analysis choices is limited. Clear documentation of outcome hierarchy, missing-data handling, and analysis populations would help readers judge how robust the posted estimates are.

15. Safety Results

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

Other (non-serious) adverse events

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

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: exacerbation of asthma (11.1%), severe osmotic symptoms (7.4%), ischaemic heart disease (3.8%), pneumonia (3.7%), diverticulitis (3.7%).

The safety summary reports serious adverse events affecting 1 of 26 participants at risk in the metformin group and 9 of 27 at risk in the placebo group. Other adverse events are reported as affecting 26 of 26 at risk in the metformin group and 22 of 27 in the placebo group. These are counts as recorded, not estimates of comparative risk adjusted for other factors. The at-risk denominators differ from the endpoint summary counts, and the registry does not explain the relationship between them.

The listed serious-event terms and percentages are exacerbation of asthma at 11.1%, severe osmotic symptoms at 7.4%, ischaemic heart disease at 3.8%, pneumonia at 3.7%, diverticulitis at 3.7%, and atypical chest pain at 3.7%. The record does not provide enough context to assign those term percentages to a particular group or to determine whether an individual could contribute more than one event. Death counts are not reported in the registry record.

Safety counts need cautious interpretation in a study of this size and duration. They describe what was recorded during the study, but do not by themselves establish why an event occurred or whether the treatment caused it. The record does not give event timing, severity definitions beyond the serious-event classification, exposure-adjusted rates, or a detailed safety analysis plan.

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

The primary result is an estimate of the difference between group mean changes in a CT-based visceral/subcutaneous fat ratio over the recorded interval. Its confidence interval includes zero, and the estimate is therefore uncertain in both direction and size. The result does not establish a clear between-group difference in this endpoint, but it also does not rule out all potentially relevant differences. The registry provides no threshold for deciding what magnitude would be clinically important.

This is a short-term measure: the endpoint is defined as 3 months minus baseline, and the intervention descriptions specify 12 weeks of treatment. The record does not report follow-up after treatment or show whether any observed changes persisted. It also does not report effects on longer-term glucocorticoid complications, clinical events, quality of life, or health-care costs, despite those outcomes appearing in the study rationale.

The secondary HOMA2-IR result concerns a separate metabolic measure and cannot be used as a substitute for the primary endpoint. The registry does not document the multiplicity plan or detailed secondary analyses, so that result should be interpreted cautiously. Overall, the posted outcome summaries offer a limited view of the study's metabolic questions rather than a complete assessment of all potential benefits and harms.

In general, randomized comparisons estimate effects of assignment under the trial's implementation and analysis conditions. Interpretation depends on how allocation was carried out, who contributed outcomes, how missing data were handled, and whether analysis decisions followed a prespecified plan. Several of these details are not reported in the registry record. The estimates are therefore best understood as the observed group summaries and their stated uncertainty, not as a definitive account of treatment effects in all people receiving glucocorticoids.

No medical recommendation follows from these posted statistics. They describe a particular study population, intervention schedule, comparator, and measurement interval. They do not establish what an individual should do, and the registry summary does not report the additional information needed to assess all clinical outcomes or longer-term consequences.

17. Why This Trial Matters Statistically

This trial is statistically interesting because it connects a mechanistic rationale in the registry summary with two distinct measured metabolic outcomes. The primary measure is an imaging-based ratio change, while the secondary measure is HOMA2-IR. Comparing these outcomes raises a useful interpretation question: a study can observe different patterns across related but nonidentical measures, and each outcome needs to be understood on its own scale and in light of its uncertainty.

The primary estimate is accompanied by a confidence interval that crosses zero. This illustrates why a point estimate and a p-value are not enough for interpretation. The interval communicates that multiple effect sizes remain compatible with the data, including values on both sides of zero. Readers can see the estimate's direction without treating that direction as certain.

The record also makes clear why reporting design and analysis information matters. It identifies randomization and parallel allocation, but does not report the original sample-size justification, detailed primary analysis, analysis population, missing-data handling, or multiplicity strategy. Those omissions limit assessment of how closely the posted summaries reflect the prespecified analysis and how much inferential weight to place on a secondary result.

Finally, the planning illustrations distinguish a future design question from a completed trial's result. Power calculations based on observed effects can help show how sample-size requirements vary with target effect assumptions, but they are not observed power and do not recover the original design rationale. This distinction is important when using a small trial to inform future research: uncertainty in the observed effect and variability should be considered rather than assuming the observed estimate will repeat.

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 registry record leaves important design and analysis details unreported. It does not give the eligibility criteria in detail, the randomization procedure, allocation concealment, or the identity of the groups covered by masking. The summary describes double-blinding, while the masking field records triple masking; the record does not reconcile these labels. This limits a detailed assessment of how bias was minimized during conduct and outcome assessment.

The primary outcome population is not described beyond the posted arm counts. Enrollment is recorded as 57, while the endpoint summaries report 19 and 21 participants in the two arms. Safety summaries give separate at-risk counts. The record does not provide a flow diagram, reasons for missing outcomes, or a definition of the analysis population. It is therefore not possible to determine from the registry whether all randomized participants were included in each analysis or how unavailable measurements were handled.

The endpoint itself is described briefly as change in visceral/subcutaneous fat measured by CT abdomen. The record does not report details of image acquisition, measurement reliability, assessor masking, or the interpretation of a change in the ratio. It also does not state a clinically meaningful threshold. These omissions make it difficult to assess measurement precision and clinical relevance beyond the reported statistical summaries.

The registry does not provide the original sample-size justification, a complete statistical analysis plan, adjustment procedures, or a multiplicity strategy. It does not report follow-up beyond the stated endpoint interval or the persistence of any changes. Safety information is also limited: event timing, causal assessments, and a detailed accounting of the listed serious-event terms are not reported. These limitations constrain interpretation; they do not establish that any particular procedure was absent.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Prevention of Metabolic Complications of Glucocorticoid Excess — NCT01319994.
• Registry record last updated 2019-04-12; status last verified 2019-01.
• Results first posted 2019-04-12.
• 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

The registry describes a completed randomized, parallel-group study of metformin versus placebo in people with iatrogenic Cushing disease receiving long-term high-dose glucocorticoids. The intervention descriptions specify 850mg TDS for 12 weeks. The primary outcome is change from baseline to 3 months in a CT abdomen ratio for visceral/subcutaneous fat.

The posted primary mean difference is 0.11, with a 95% confidence interval from -0.017 to 0.237 and an unadjusted p-value of 0.09. One secondary outcome, HOMA2-IR, is listed. The registry record does not report the original sample-size rationale, detailed analysis plan, missing-data approach, or multiplicity strategy. The estimates should be interpreted as short-term outcome summaries with material uncertainty and incomplete analysis documentation.