On Versus Off Pump Myocardial Revascularization Study: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for On Versus Off Pump Myocardial Revascularization Study (NCT01290952), a randomized phase 4 study. The primary outcome is Number of Patients With Post-operative Combined Endpoint (i.e. With One or More of the Following).

2. Clinical Question

The question concerns the frequency of a combined postoperative endpoint, not the frequency of each component separately. A patient is counted as having the endpoint if at least one listed event occurred. The record does not report the separate component counts, so the combined outcome cannot show which event types account for the observed group difference.

The comparison is between surgical strategies, rather than between surgery and no surgery. The clinical question also includes completeness and modality of revascularization, operative and postoperative results, and one-year clinical outcomes in its summary. However, the posted primary endpoint described in the results is the 30-day combined postoperative endpoint; outcomes beyond that result should not be inferred from it.

3. Trial Design

This is a randomized, parallel-group, phase 4 study. The registry record describes no masking. Participants were assigned to off-pump bypass surgery or on-pump bypass surgery. Enrollment was 411. The study status is completed, with a recorded start of 2006-09 and primary completion of 2010-06.

The off-pump procedure was described as OPCAB using a mandatory stabilization device, with a heart positioner advisable but not mandatory. The comparator was coronary artery bypass graft surgery with cardiopulmonary bypass, identified as CPB/CAB. The record does not provide further procedural details, such as whether particular operative choices were standardized across participating clinicians.

The primary outcome is a count of participants with one or more events in a combined endpoint during 30 days. The registry lists 204 participants in the off-pump group and 207 in the on-pump group for this outcome. It lists 13 endpoint events in the off-pump group and 26 in the on-pump group. These are participant counts, not event totals that could include multiple events per person.

The record also lists a 30-day secondary combined endpoint and adverse-event counts. The secondary outcome is described as a combined endpoint, but its component definition is not reported in the registry record. The record names Medtronic Italia as sponsor. It does not report the trial's original sample-size justification, its detailed allocation procedures, or its analysis populations.

Random allocation is useful because, in expectation, it makes the groups comparable at the time of assignment. It does not guarantee that every measured or unmeasured characteristic is balanced in a particular trial. The registry record does not give enough detail to assess the allocation sequence, concealment procedures, or any stratification used in the randomization.

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: 630 patients was the planned estimated sample size needed to test the null hypothesis. An interim analysis was scheduled at 400 enrolled patients, to verify the null hypothesis used for the sample size calculation. A p\<0.0294 was considered statistically significant to reject the null hypothesis, thus study enrollment was stopped at 411 patients.

Overall Study

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 Patients With Post-operative Combined Endpoint (i.e. With One or More of the Following), measured over 30 days.

The primary endpoint counts the number of participants who experienced at least one event in a specified postoperative composite within 30 days. Its components are operative mortality, myocardial infarction, postoperative neurological complications, renal failure, acute respiratory distress syndrome, and bleeding. A participant meeting more than one component is still included once in the count of patients with the combined endpoint.

A composite endpoint can capture a broader range of postoperative problems in a single outcome. It can also make an overall comparison easier to interpret as a measure of whether any listed complication occurred. Its meaning depends on which components are included and how clinically different those components may be. A combined count does not establish that the groups differed in every component, or identify which component contributed most to the total.

The endpoint is reported for 30 days, so it describes events during that timeframe rather than later outcomes. The registry record does not report component-specific counts, definitions for adjudicating each component, or further detail about how the endpoint was assessed. Those details would help readers judge the consistency and clinical meaning of the composite. The result should therefore be read as a comparison of participants with one or more listed events, not as a separate estimate for mortality, infarction, neurological complications, renal failure, respiratory distress, or bleeding.

7. Results Posted in the Registry

• On-pump: 12.6% (26/207) versus 6.4% (13/204) on control; risk difference 6.2 percentage points (95% CI 0.6 to 11.8), risk ratio 1.97 (1.04–3.73); unadjusted two-proportion z-test p = 0.032.

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.

Number of Patients With Secondary Combined Endpoint (i.e. With One or More of the Following)

• 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:
  • Off-pump Bypass Surgery: 32.8% (67/204) versus 35.3% (73/207) on control; risk difference -2.4 percentage points (95% CI -11.6 to 6.7), risk ratio 0.93 (0.71–1.22); unadjusted two-proportion z-test p = 0.604.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Off-pump Bypass Surgery and the control. The interval gives the range of effects that remain compatible with the data.

The registry reports one secondary combined endpoint, assessed at 30 days. Its comparison does not show a clear separation between the groups: the risk-difference interval includes no difference and the unadjusted p-value is 0.604. This is a less precise pattern than a result that would sharply distinguish the groups, and it does not establish equivalence or prove that the groups have identical outcomes.

The primary and secondary comparisons address separate combined outcomes. The primary result has an interval excluding no difference, whereas the secondary interval includes no difference and allows effects in either direction. This contrast does not demonstrate that the primary result is more important, nor does it identify a biological or procedural explanation. The secondary endpoint’s component definition is not reported in the registry record, making it difficult to evaluate how its clinical content relates to the primary composite.

The record reports one secondary outcome and no reported analyses for it. It does not describe a prespecified hierarchy of outcomes, a multiplicity adjustment, or a plan for interpreting several outcome tests together. When multiple endpoints are examined, the chance of at least one apparently unusual result can increase. For this reason, unadjusted secondary results generally carry less confirmatory weight unless the analysis plan and role of the outcomes are clear.

The secondary estimate can still be informative as a description of the posted data, but it should be interpreted alongside its uncertainty and the missing definition and analysis details. It does not overturn the primary estimate, and the primary estimate should not be used to fill in the missing information about the secondary outcome. Neither comparison provides component-level results or establishes what happened after the stated 30-day timeframe.

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

• Number of Patients With Secondary Combined Endpoint (i.e. With One or More of the Following)

9. Statistical Interpretation

10. Statistical Methods Explained

General: A risk difference compares the proportion of participants with an outcome between two groups by subtracting one group’s proportion from the other’s. A value of zero corresponds to equal observed proportions. The sign depends on the order of the groups in the comparison, so the stated direction matters when interpreting a positive or negative estimate.

For the primary outcome, the registry gives the comparison as on-pump relative to off-pump surgery. The point estimate is on the positive side of no difference, and the confidence interval does not include zero. The posted risk difference is 0.062, with a confidence interval from 0.006 to 0.118. These values are registry-posted estimates; they should not be confused with a separately adjusted treatment effect, because adjusted analyses are not reported in the registry record.

General: A confidence interval describes a range of estimates compatible with the observed data under the method used. It communicates uncertainty around an estimate; it is not a range that guarantees the true effect lies within it. When a risk-difference interval includes zero, the data are compatible with no difference under that interval method. When it excludes zero, the interval indicates that no difference is outside that range, but this alone does not measure clinical importance.

The record also gives relative measures for the primary comparison. The relative risk is 1.971, with a confidence interval from 1.042 to 3.727. The odds ratio is 2.11, with a confidence interval from 1.052 to 4.234. A relative risk compares event proportions as a ratio; an odds ratio compares event odds. These measures use different scales from a risk difference and are not interchangeable. In particular, the magnitude of an odds ratio does not directly express a difference in the number of participants affected.

The primary unadjusted p-value is 0.032. General: A p-value measures how unusual data at least as incompatible with a null hypothesis would be under the assumptions of a specified statistical test. It is not the probability that the null hypothesis is true, nor does it describe the size or clinical importance of an effect. The registry does not report the test specification or a detailed analysis plan, so the p-value is best treated as the posted unadjusted result rather than as a complete account of the analysis.

For the secondary endpoint, the reported risk difference is -0.024, with a confidence interval from -0.116 to 0.067, and the unadjusted p-value is 0.604. Its relative risk is 0.931, with a confidence interval from 0.711 to 1.219. Its odds ratio is 0.898, with a confidence interval from 0.597 to 1.35. The risk-difference interval includes zero; the relative-measure intervals include one, the corresponding null value for those ratios. Taken together, these measures do not provide a precise distinction between the groups for this secondary endpoint.

General: Binary outcomes, such as whether a participant had one or more events, are commonly described with counts and proportions. A risk difference is often straightforward to interpret in terms of absolute frequency, while relative measures express how event frequency compares proportionally. Reporting more than one measure can help convey different aspects of the comparison, but it does not remove uncertainty or resolve limitations in outcome definition.

General: Over-dispersion is a concern when observed variability is greater than the statistical model expects. It can make standard errors too small and confidence intervals too narrow if the model does not allow for the extra variability. The posted primary outcome is a participant-level binary composite, and the registry record does not describe a model that accounts for over-dispersion. The issue is therefore not something that can be assessed from the record; it is a general consideration when the chosen model assumes less variability than the data-generating process may have.

The record lists no reported analyses for the secondary outcome. The displayed comparison statistics are not accompanied by a description of covariate adjustment, missing-data handling, or sensitivity analyses. Those details are not reported in the registry record. The primary comparison is therefore interpreted as the posted unadjusted contrast and not as a claim that every possible analysis would give the same result.

The registry also includes planning illustrations based on the observed effects. These are not retrospective measures of the trial’s power, and they do not establish whether the study was adequately designed for its original aims. The original sample-size assumptions and justification are not reported in the registry record. General: A planning calculation uses assumptions about a target effect, error rates, allocation, and an analysis method to illustrate the sample size that might be needed. It cannot substitute for the trial’s original design documentation or establish the probability that a result is true.

11. Confidence Intervals and Precision

The precision of the primary estimate is best judged by looking at its confidence interval, not just the point estimate or p-value. The posted risk-difference interval runs from 0.006 to 0.118. It is entirely above zero, but its span also shows uncertainty about the size of the difference. The relative-risk interval, from 1.042 to 3.727, likewise lies above its null value of one while covering a broad range of possible relative effects. The estimate points to a difference in the direction of more primary endpoint events in the on-pump group, but the exact magnitude is not pinned down narrowly.

The secondary risk-difference interval runs from -0.116 to 0.067, crossing zero. Its relative-risk interval, from 0.711 to 1.219, crosses one. These ranges are compatible with differences in either direction, including no difference, so the secondary estimate is uncertain about both direction and size.

General: Precision concerns how narrowly an estimate is bounded by its uncertainty interval. A narrow interval can indicate more precision than a wide interval, but precision does not establish that an estimate is unbiased or clinically important. The interval depends on the data and the statistical method; the registry does not report enough methodological detail to independently assess every assumption behind the posted intervals.

The primary event counts are modest relative to the number enrolled, and the interval width makes clear that substantial uncertainty remains about the magnitude. The registry does not provide component-specific intervals, so precision cannot be assessed separately for each event type in the composite. It also does not provide a one-year estimate in the posted results. Conclusions about the precision of later clinical outcomes are therefore not supported by these 30-day results.

12. Planning a Similar Trial: Sample Size

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

The planning figures are participants per arm for the binary outcomes in this record. They are not total event counts. The illustrations use two-sided significance level 0.05, equal allocation between the two arms, and a normal approximation. The target effect is set to a stated fraction of the observed effect. The trial’s own original sample-size justification and design assumptions are not reported in the registry record.

The 80% power column gives an illustrative number of participants per arm for a design with an 80% chance of detecting the specified effect under the stated planning assumptions, if that effect and those assumptions were correct. The 90% power column gives the corresponding planning number for a 90% chance. These are design concepts, not guarantees about what a future study will find. The figures are planning illustrations, not observed power.

For the primary endpoint, the illustration based on 100% of the observed effect lists 351 participants per arm for 80% power and 469 per arm for 90% power. Planning for 75% of the observed effect gives 578 per arm for 80% power and 773 per arm for 90% power. Planning for 50% of the observed effect gives 1,195 per arm for 80% power and 1,599 per arm for 90% power.

The secondary endpoint illustrations are much larger: the 100% effect row lists 6,006 participants per arm for 80% power and 8,040 per arm for 90% power; the 75% row lists 10,724 and 14,355 per arm; and the 50% row lists 24,229 and 32,436 per arm, respectively. These figures follow from the observed effect and the stated calculation assumptions, not from the original trial design.

General: Smaller target effects generally require more participants to distinguish them from random variation, which is why planning for a smaller fraction of the observed effect yields larger sample-size illustrations. The observed effect can itself be unstable, particularly when estimated in a modest study, so these calculations should not be treated as a recommendation or as evidence about the trial’s original planning rationale.

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 = 0.064; treatment proportion p₁ = 0.126; average p̄ = 0.095.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.4140 = 0.8115.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4117 = 0.3465.
4. n = (0.8115 + 0.3465)² / (0.0619)² = 350.2, rounded up to 351 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 <- 0.0637254901960784                          # control proportion
p1 <- 0.1256038647343                          # 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(1290952)
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 = 351 (80% power), 469 (90% power)
 75% of observed effect: n per arm = 578 (80% power), 773 (90% power)
 50% of observed effect: n per arm = 1,195 (80% power), 1,599 (90% power)
power.prop.test: 350.2 
Simulated power at n = 351 per arm: 0.811 (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. Multiplicity, Missing Data and Analysis Populations

The registry record does not report a multiplicity plan. It does not say whether the primary endpoint was the sole confirmatory outcome, whether secondary outcomes were ordered in a hierarchy, or whether any adjustment was planned for testing more than one outcome. Without those details, the unadjusted p-values should not be interpreted as if a family-wise error strategy or other multiplicity procedure had been applied.

General: Multiplicity arises when investigators make several statistical comparisons or assess several outcomes. Even when each test uses the same threshold, a larger collection of tests can increase the chance of at least one result appearing notable by chance. Adjustment methods and prespecified testing strategies can address this issue, but they may change how results are interpreted. No such method is reported in the registry record.

The record also does not report how missing outcome data were handled, whether all randomized participants were included in the analysis, or whether the primary analysis followed an intention-to-treat principle. The registry lists outcome denominators of 204 for the off-pump group and 207 for the on-pump group, but it does not explain whether those numbers represent all randomized participants or an analyzed subset. Missing-data patterns and any imputation or sensitivity analysis are not reported in the registry record.

Analysis populations are also not described. The record does not indicate whether there were per-protocol, safety, or other analysis sets, or how participants who did not receive their assigned procedure were classified. The randomized allocation is an important design feature, but assessment of the analysis requires knowing how allocation was carried through to outcome analysis.

These omissions do not show that the trial lacked suitable procedures; they mean the registry record does not provide the detail needed to evaluate them. A full protocol or statistical analysis report could clarify these issues, but such information is not reported in the registry record.

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 2% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: mace (7.7%), overall mortality (6.8%).

The adverse-event information lists serious adverse events affecting 16 of 204 participants in the off-pump group and 30 of 207 in the on-pump group. Other adverse events are listed for 72 of 204 and 79 of 207 participants, respectively. These are group counts and denominators as recorded; they should be read separately from the primary postoperative composite, whose component list is specified independently.

The registry lists MACE at 7.7% and overall mortality at 6.8% among the top serious adverse-event terms. It does not assign these two percentages to a particular arm in the displayed record, so they should not be interpreted as arm-specific rates. The record does not provide death counts in the adverse-event summary, and does not give detailed definitions or severity breakdowns for these terms.

Serious adverse-event counts do not by themselves show whether events were caused by a procedure. The record does not provide an adjusted safety comparison, event timing details, or a formal statistical analysis of these adverse-event counts. Differences in the recorded counts are descriptive; the registry information is not sufficient to establish causation or to determine the safety profile beyond the reported terms and groups.

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

The posted primary result describes more participants with at least one component of the 30-day postoperative composite in the on-pump group than in the off-pump group. The risk-difference interval excludes zero, and the unadjusted p-value is 0.032. The result is evidence of a group difference in the recorded primary composite under the reported comparison, while the confidence intervals show that the size of that difference remains uncertain.

It does not show that every component of the composite differed, because separate component counts are not reported. It does not establish a difference in any single component, including mortality or myocardial infarction. It also does not establish what happened after 30 days. The registry summary mentions one-year clinical outcomes as an aim, but corresponding one-year results are not reported in the record.

The secondary combined outcome has an interval that includes no difference and an unadjusted p-value of 0.604. That is not evidence that the two procedures are equivalent. A result that does not distinguish groups may reflect a small effect, imprecision, or other factors; the registry result alone cannot determine which explanation applies. The secondary endpoint’s component definition is not reported in the registry record.

General: A trial result is an estimate for the participants and outcomes studied, subject to uncertainty and the study’s design and analysis. A randomized comparison can support a causal interpretation when allocation and analysis are properly implemented, but the registry record does not provide the full details needed to assess all relevant assumptions. The result should not be extended automatically to populations, procedures, or outcomes not described in the record.

These statistics are not a treatment recommendation. They describe the registry’s posted comparison and its precision. The result does not establish that either approach is universally preferable, does not resolve the component-level pattern, and does not substitute for evidence on longer-term outcomes or other clinical considerations.

17. Why This Trial Matters Statistically

This trial illustrates why the definition of a clinical endpoint matters as much as the headline comparison. The primary outcome combines several postoperative events into a participant-level count. That approach can provide a compact summary of complications, but the combined estimate cannot reveal whether its components show a consistent pattern or whether one component dominates. Component-specific reporting would be needed to answer those questions.

The registry also illustrates the value of reading a point estimate together with its interval. The primary interval excludes no difference, yet its range indicates uncertainty about the magnitude. The secondary interval includes no difference and supports a less decisive interpretation. P-values alone would not convey either the size or precision of these comparisons.

Comparing absolute and relative measures gives different perspectives on the same data. The risk difference describes an absolute contrast in event proportions, while relative risk and odds ratio express contrasts on ratio scales. Their interpretation depends on the measure and the order of the groups. Looking across measures can help readers avoid treating one statistic as a complete description of the evidence.

Finally, the record shows the limits of registry-level results. Randomization and group counts are informative, but absent details about missing data, analysis populations, multiplicity, and the original sample-size justification restrict what can be independently assessed. The planning illustrations are not a substitute for the trial’s own design rationale. Transparent methods and component-level outcome reporting are important for judging how robustly a clinical comparison answers its intended question.

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 endpoint is a composite, and the registry record gives no separate counts for operative mortality, myocardial infarction, neurological complications, renal failure, acute respiratory distress syndrome, or bleeding. That prevents assessment of which components account for the primary difference and whether the components have similar importance. The secondary endpoint is also described as combined, but its component definition is not reported in the registry record.

The posted results focus on a 30-day primary endpoint. Although the study summary refers to one-year clinical outcomes and completeness and modality of revascularization, results for those aims are not reported in the registry record. No longer-term comparison should be inferred from the 30-day endpoint.

The record does not report the original sample-size justification, detailed analysis plan, missing-data handling, analysis populations, or multiplicity procedures. It also does not describe allocation concealment, stratification, or the statistical methods in enough detail to assess these aspects of the trial. These are limitations of what can be evaluated from the registry information, not proof that the trial did not address them.

The procedural descriptions provide some detail about the off-pump strategy but do not report further variation in surgical practice or adherence. The record does not supply component-level adverse-event details, cause attribution, or a full safety analysis. Finally, the results apply to the high-risk patients referred for primary bypass surgery described in the trial record; the registry information does not establish how well the estimates generalize to other populations or care settings.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: On Versus Off Pump Myocardial Revascularization Study — NCT01290952.
• Registry record last updated 2016-11-21; status last verified 2016-09.
• Results first posted 2016-11-21.
• 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 record describes a completed randomized, parallel-group, phase 4 study with no masking. It enrolled 411 high-risk patients referred for primary coronary artery bypass surgery and compared off-pump bypass surgery with bypass surgery using cardiopulmonary bypass.

The primary outcome was the number of participants with one or more specified postoperative events within 30 days. The record reports 13 events among 204 off-pump participants and 26 among 207 on-pump participants. The posted unadjusted primary comparison has a risk-difference confidence interval excluding no difference, with p = 0.032. The secondary 30-day combined outcome has an unadjusted p-value of 0.604 and an interval that includes no difference.

Component-specific results, one-year outcome results, the original sample-size rationale, and key analysis details are not reported in the registry record. Interpretation should remain focused on the posted 30-day composite estimates and their uncertainty.