Pablo Lamelas –
In the recent years several randomized trials comparing complete vs culprit-only revascularization were published, in which many of them were ¨positive¨. Then, do we have a definitive answer? or we need to wait? In this article we summarize the results and methodological weaknesses of the current literature.
Randomized trials meta-analysis
Among the 8 randomized trials to date on this topic, complete revascularization was associated with a significant reduction in cardiovascular mortality (OR 0.51, 95% CI 0.31 – 0.84, p = 0.009), myocardial infarction (OR 0.69, 95% CI 0.48 – 0.98, p = 0.04), and new revascularization (OR 0.37, 95% CI 0.29 – 0.47, p < 0.001).
A quick look to those results sound convincing, but are they really?
Limitations of current literature
Although statistical heterogeneity (that means, heterogeneity detected by statistical tests, like Cochran Q test or I-squared used in meta-analysis) was not substantial, a quick look to the details of each study makes us wonder that some clinical heterogeneity (different ways to define the population, intervention delivery or comparator) may exist.
To name a few, definition of non-culprit lesions as targets for revascularization ranged from > 50% stenosis to systematic use of FFR. Staged PCI was was done in the same STEMI procedure in some studies, while others in-hospital only in some of the trials or even after discharge. DES use ranged from less than 10% use to more than 95% among trials. Some of these studies discouraged the use of stress testing, which does not only do not represent usual practice in patients with culprit-only primary PCI (residual disease present) but also causes clinical heterogeneity in the comparator group performance between trials.
When pooling data from large trials, clinical heterogeneity is usually expressed statistically (tests for heterogeneity likely show “statistically significant” heterogeneity). On the other hand, when pooling data from studies that were not individually powered for the outcomes of interest (death or myocardial infarction for instance) may express some degree of “hidden heterogeneity”: in other words, clinical heterogeneity that cannot be detected statistically because is inherently underpowered for those outcomes. Thats one of the potential issues of meta-analysis composed from small (not individually powered for the outcomes of interest) trials only.
Is there also methodological heterogeneity too? I think yes. For instance, one influential study was stopped early for benefit. Studies with different degree of bias can induce methodological heterogeneity. Will discuss this below.
New revascularization outcome
The outcome measure that was clearly in reduced by complete revascularization treatment arm was new revascularization. Similar to what happened in FAME II trial, think is fair to compare new revascularization when one group has complete revascularization at baseline and the other one left with angiographically and/or physiologically (ie, FFR or iFR) significant lesions in an open-label trial?
Going to the extreme example, would you feel comfortable interpreting a trial which observed that systematic preventive appendectomy in asymptomatic people drastically reduced future appendectomies compared to a group without preventive appendectomies? The difference in this example is that someone with a successful appendectomy cannot suffer from appendicitis, when a completely revascularized patient may receive further coronary procedures due to progression of coronary artery disease, stent restenosis or stent thrombosis.
I am not insinuating that new revascularization is not an important outcome measure, the problem is its interpretation in this context, when the outcome is somewhat delivered at baseline in one group. And equally conflictive is to include it in composite outcomes (typically, death, stroke and repeat revascularization together) causing misinformation and early stop of trials for efficacy.
Early stop for efficacy
PRAMI trial was stopped early for efficacy, while the CVLPRIT trial was conceived as a pilot study and then completed after enrolling 6 more centers in the UK.
What is the problem with stopping early for efficacy? Basically: the effect is usually exaggerated, the point estimate (the risk reduction observed) likely not real. Does not mean that the intervention does not work, but at likely not that much.
Stuart Pocock summarized the adverse effects of early stop for efficacy in 1992:
- Lack of credibility: each of these small trials alone is not convincing.
- Lack of realism: the dramatic reduction in events is difficult to believe. For instance, evidence to date of preventive PCI in stable patients does not suggest even a hint of mortality benefit, and here the meta-analysis shows a 50% relative risk reduction in cardiovascular death.
- Imprecision: none of this trials have precise estimates for death or myocardial infarction, the two outcomes that really matters in this issue
- Bias: this result maybe a “random high”, a random exaggerated benefit.
- Speed: there is no enough time to see longer term impact, or study adverse effects, and costs.
- Pressure: seemingly fantastic results puts pressure over guidelines developers and healthcare systems.
- Mistakes: early stop for efficacy cannot rule out that the intervention actually does’t work at all (not even a very small benefit, or less likely cause harm).
We know that two studies with the same p-value may have different degree of robustness. Those studies composed with smaller number of events are called “fragile”. Mike Walsh with other colleagues from McMaster University developed a tool to quantify it, called the fragility index. In simple words, is the number of events added (imputed) the intervention group (assuming the outcome is an adverse event and the trial was “positive”) to make the p-value > 0.05. The higher the index, the more robust are the results, here you can find a calculator.
There is no consensus in how much is considered a non-fragile result, but we may agree that under 5 is a weak trial, while over 10 would be reasonable to say not-fragile. To give examples from cardiovascular literature, PLATO trial death-stroke-MI fragility index was 85, RELY (Dabigatran 150 mg vs Warfarin) for stroke was 30. Well, the death-stroke combined fragility index of PRAMI trial was 3.
Do we know the answer then?
Despite of very promising results from the meta-analysis showed above, it is pretty clear that this evidence has many limitations before be jump doing complete revascularization in STEMI patients.
Soon the results of the COMPLETE trial will be out, which enrolled over 4,000 patients. This study has two co-primary outcomes, one with and the other without new revascularization. We hope this trial will provide more insight in how we should manage these patients.
One Reply to “Complete vs culprit-only revascularization in STEMI”