Impact of Periprocedural Myocardial Biomarker Elevation on Mortality Following Elective Percutaneous Coronary Intervention - study results & interpretation

Good morning everyone,

We’ve come across the paper on ‘Impact of Periprocedural Myocardial Biomarker Elevation on Mortality Following Elective Percutaneous Coronary Intervention’ from Garcia-Garcia et al published in JACC: Cardiovascular Intervention and scratched our heads as to the overall results and interpretation. The paper is available here:

The authors have pooled 5 coronary stent trials and 1 large registry - all patients were stable, with ‘normal’ baseline biomarkers (notably CK-MB and cTn); different cut-offs were compared to assess the prognostic significance of biomarker elevation following coronary intervention. The authors concluded that CK-MB was a better predictor of mortality after 1 year than cTn.

The conclusion was based on, as far as I can tell, two main findings:

  1. Figure 1 depicts one-year mortality rates depending on the biomarker range, categorised into ratios of CK-MB/cTn ratios of ULN.
  2. The Cox models: As per their methods section, the biomarkers were forced into two models - model A using CK-MB at ≥10 x ULN, model B using cTn ≥70 x ULN. The ratios are derived from the SCAI or Universal Definition of MI definitions.

I feel this analysis could have been improved dramatically to provide more granularity. A major limitation is that two biomarkers with different release kinetics are compared at the same timepoint - cTn only peaks somewhere between 24-36 hours, and you would not expect elective patients to still be in hospital for a ‘peak sample’; CK-MB rises faster and peaks earlier.

The ULN ratios are rather arbitrary, and whilst they are ‘as good as it gets’ currently, when it comes to guideline-endorsement, afaik they were not derived based on a biological concept (or equivalence, for that matter).

With respect to the Cox models, it’s odd to see different variables entered into the two multivariate models - model A uses age, prior MI, lesion complexity, CK-MB ratio, hyperlipidaemia and DM. I would have expected model B to just swap CK-MB for cTn ratio, but the model has also ‘gained’ prior CABG and sex - surely, based on the univeriate analysis, both of them should have been entered into both models? Can somebody think of a genuine reason as to why not?

An interesting detail is that having a diagnosis of hyperlipidaemia appears to lower your risk by almost half - I don’t see that mentioned in the discussion either.

Would be keen to hear your opinions on the points raised above.


Hi Tom,

Thanks for posting, and to Frank for directing me here from Twitter. You have raised several important points about this paper a number of which occurred to me on first inspection.

One issue I felt was counterintuitive was the identification of a group which was CK-MB +ve, cTn -ve, and I considered e-mailing Paul Collinson to get his views from a pathophysiological point of view. I would have thought any patient with CK-MB elevation should demonstrate co-existent elevation in cardiac troponin concentration? Unless as you point out, they have been measured at a timepoint in which one assay has yet to peak, or has already peaked. Therefore, I suspect sample timing has biased the results towards CK-MB.

Rather than focusing on the ULN a ‘better’ analysis might have been a regression model with absolute values of each log transformed biomarker as a continuous variable. As we have discussed before, I think its extremely unlikely there would be a threshold effect, and we have moved on from the ‘positive vs negative’ mentality. For the models presented, I strongly agree that given they are presenting a direct comparison of CK-MB and troponin, the same co-variates should have been employed in both. Indeed they could have presented a multi-variable model including CK-MB and Trop?

With regard to hyperlipidaemia, I wonder how this variable was defined. If simply defined by statin prescription that could confound the result?

This paper absolutely merits proper evaluation as it could have a major bearing on the definition of peri-procedural biomarker elevation in future international definitions. I will give it a thorough read again and see if I can identify any other issues.


Thanks, Andrew! I couldn’t agree more on the sentiments regarding using e.g. log-transformation of the continuous biomarker. I had a similar thought when I realised they’re challenging the current guidelines - and as such employed the guideline-recommended thresholds (as ratios of ULN) to compare the two biomarkers.

Nevertheless, this appears to be apples & oranges, I worry as to why the different cox models were employed (and accepted throughout the peer-review process).

Excellent thought - I don’t think this was stated, might have to go back to the original publication sources to find out.

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I enjoyed reading the previous discussion on this important paper.

Basically, the authors of the discussed paper have to be complimented for managing the difficult task of pooling patient-level data of 5 different studies.

In regard to the previous discussion, I also do not understand why the covariates of Model A and Model B differ. In my opinion, this is counter-intuitive and makes the interpretation of the results difficult. Moreover, the rationale for covariate selection per se is unknown?

I would be also interested in data regarding the timing of the post-procedural blood sampling for the reported biomarkers.

However, the main question on my mind is: Would not a multi-level model have been more appropriate for an analysis pooling patient-level data of 5 different studies?

Thanks for your thoughts Alexander. Multilevel analysis of…the biomarkers?

I was thinking about a multilevel Cox regression model for the prediction of 1-year mortality (Table 6) to ensure clustering of patient within studies.

Each patient was enrolled in one of the pooled studies. Each study might be slightly different. Therefore, the baseline risk and the susceptibility to suffer myocardial injury periprocedurally might be different between the pooled studies.

What do statisticians think about this?

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I thought I’d share the letter we’d sent to the editor with respect to the point discussed here:

I am not sure the response of the authors clarifies a lot, but at least we highlighted some issues surrounding the paper.