The premise for this question rests on the implications for further management. If the two nodules are synchronous, say 2 lesions that are T1 N0 M0 and T1 N0 M0 then it is assumed that complete resection of both will lead to a survival of a T1 N0 M0 tumour. On the other hand, if one is metastatic, then surgical resection would achieve survival of a T1 N0 M1 lesion.

Martini considered a second nodule to be synchronous if it was in situ, a different cell type and did not share the same lymph supply of the (presumably) distal nodule.(1) If these criteria were fufilled, the tumours could be considered as synchronous. There was a comment during the discussions that Martini made up these criteria, but if you think about it, they do make some sense.

The 6th revision of the UICC classification for lung cancer does not differentiate between synchronous and metastatic but considers a seperate nodule in the same lobe as T4 and in a different lobe as M1.(2) On conventional selection criteria patients with stage IIIB and IV are not considered for surgery.

I think all these arguments are flawed...

So where does that leave us?

I think we have no means to realiably distingush between metastatic and synchronous lesions, these patients do not have a post operative prognosis comparable to clinical stage IIIB / IV, but neither do they have a prognosis of two separate lesions - the post operative prognosis lies somewhere in between. The decision to proceed to surgery is ambigious and revolves around a concept that I love to survey: what is a 5 year survival that you and the patient would consider worthwhile to undertake the risks of a surgical operation (or two)?

The question itself is loaded, because it centres either around a relative benefit compared to untreated disease, or an absolute percentage survival. The former cannot be quantified, because we have no information on the outcome of comprative patients treated only by medical therapy, and therefore decisions are usually made on absolute survival. The conventional cut off is 40% or more (IIB), but the patient and surgeon may consider 30 or even 20% or more as worthwile, sadly many decisions are dichotomised into synchronuous - operate, metastatic - don’t operate without taking into account the ambiguity of classification, staging, post surgical outcome and most importantly - patient choice.

References

1. Martini N, Melamed MR. Multiple primary lung cancers. J Thorac Cardiovasc Surg. Oct 1975;70(4):606-612.
2. Mountain CF. Revisions in the International System for Staging Lung Cancer. Chest. Jun 1997;111(6):1710-1717.
3. Battafarano RJ, Meyers BF, Guthrie TJ, Cooper JD, Patterson GA. Surgical resection of multifocal non-Small cell lung cancer is associated with prolonged survival. Ann Thorac Surg. October 1, 2002 2002;74(4):988-994.
4. Trousse D, Barlesi F, Loundou A, Tasei AM, Doddoli C, Giudicelli R, Astoul P, Fuentes P, Thomas P. Synchronous multiple primary lung cancer: an increasing clinical occurrence requiring multidisciplinary management. J Thorac Cardiovasc Surg. May 2007;133(5):1193-1200.

While monitoring for complications, the FDA states that it still currently “believes that coronary drug-eluting stents remain safe and effective when used for the FDA-approved indications”. Furthermore, the meta-analysis by Camenzind (presented to the 2006 European Society of Cardiology Annual Meeting) reported death and Q-wave MI increased in drug-eluting to bare-metal stents. The conclusions imply selective return to bare metal stents as opposed to a mass exodus towards coronary artery surgery.

As a group, we naturally extol what we like to hear and ignore what we don’t. Before peering over the fence at our neighbor’s gardens, maybe we should look at the results off pump graft patency. This month (December 2006) in the Journal of Thoracic and Cardiovascular Surgery, we reported a significant increase in graft occlusion in randomised trials of off pump compared to conventional surgery, but maybe you don’t really want to hear about that…

It was an article highlighted for CME, probably due to educational value and clinical importance, but certainly not on the quality of statistical reporting. It is surprising that an article of such standing reached the printing press with P=0.00 reported throughout the manuscript. It suggests that the authors and reviewers were unaware of the implications.

A P value is the probability of observing the given results or more extreme values given that there is no true difference (ie the “the null hypothesis is true”). Therefore P=0.00 means that the probability of observing the results or more extreme values is zero given that there is no true difference, which in itself is impossible. What the authors really meant was that the probability was less than 1% (ie P<0.01).

The tables in the manuscript were confusing, as they reported the percentages without actual numbers. Furthermore, the categories in some tables were subdivided by disease (eg 30-day mortality, table 7), therefore and the reported percentages had nothing to do with the denominators listed at the top of the table (BITA n=4462 and SITA n=4204).

The authors used multivariate instead of multivariable. A multivariable (correct term) analysis refers to one dependant variable and many explanatory variables, as per the standard logistic regression. A multivariate analysis means that there were more than one dependant variable that was analysed simultaneously, this is rarely used in medical literature, and consists of techniques such as principal component analysis and factor analysis.

Many other questionable aspects of the statistical reporting aside, I couldn’t help but feel that the article was reported in a manner biased towards BITA usage. The conclusion included:

“CABG using both ITAs can be performed routinely with good clinical results and low mortality. Compared with single ITA grafting, sternal and bleeding complications were slightly increased...”

which, after reading the paper I would rephrase as…

“CABG using both ITAs can be performed routinely (for perceived benefits from non-randomised observational studies that have usually performed BITA on selected healthier, lower risk patients) if you are willing to accept a longer duration of surgery, bypass time, cross clamp time, more bleeding, 4.8 fold increase in re-thoracotomy rate (why re-thoracotomy instead of re-sternotomy?), 2 fold increase sternal dehiscence and 3.5 fold increase in mediastinitis, with low mortality ”

Just because the access is smaller, it does not make what is done inside the body cavity less traumatic or invasive. If an equivalent procedure is performed, it will be as equally invasive. What saving is the “trauma” associated with a 4 inch versus an 8 inch sternotomy or the cumulative sum of 3 x 1.5 inch port sites versus a 8 inch limited thoracotomy, or a 6 inch limited thoracocomy and 2 x 1.5 inch port sites with VATS assistance versus 10 inch thoracotomy? If the procedure takes longer than conventional access surgery, would the duration of surgical trauma result in greater overall physiologic stress?

Many surgeons use the minimally invasive route as a self / institution promoting strategy hoping to gain more referrals and better patient acceptance for procedures where primary efficacy and safety are usually unconfirmed by randomised trials. Indeed, the primary aim is often forgotten in pursuit of surrogate marker to justify the performance of a possibly more expensive, less accessible, less complete and more compromising (during the initial learning curve) procedure. Why do most trials on VATS surgery for pneumothorax report pain and length of hospital stay instead of recurrence rates, and observation studies on minimal access revascularisation report pain and hospital stay instead of angiography graft patency, recurrence of angina and survival?

Reports of new techniques are often undertaken by enthusiasts in the field, who have a vested interested in proving what they are doing is better, and are often reviewers of papers related to these techniques, therefore how many papers critical to what they do would receive a good review?

My own views are that state of the art is not necessarily better, efficacy must be proven in the primary reasons for surgery before patients and referring physicians are “sold” the soft benefits of minimal access surgery.

Ok, so surgical revascularisation rates are down and percutaneous coronary intervention rates are on the rise, but don’t worry, there’s always aortic valve surgery, the second most commonly performed operation in cardiac surgery?

Hate to burst your bubble, but read it and weep, 50 percutaneous valve implants for aortic stenosis, regurgitation and failed prosthetic valves.

Ah ha! You may exclaim that the founder of CoreValve is a cardiac surgeon. He may have been involved in the development of the percutaneous valve! So, we will be able to participate in this new technology? Sure, all we need is for suitable patients to be referred for…. Oh! they already are experts in percutaneous interventions...

In the New England Journal of Medicine, the Perioperative Ischaemia Research Group just published the results of a large observational study encouraging readers not to use aprotinin after cardiac surgery. One of the main reasons cited in the paper was a doubling in the risk of renal dysfunction and renal failure.

The study is to be commended on the large sample size, an impressive 4374 patients in 69 institutions across the world. Whilst we, as readers and reviewers are often wary about conclusions based on small sample sizes concluding no difference when a true difference might exist, why don’t we display a similar scepticism about large studies that conclude a difference when none might exist?

Big is not always better, the authors state that in this setting, a randomised trial would be ideal but would be difficult “if not impossible” to conduct, and observational studies when sufficiently large may offer critical insights even in light of recognized limitations.

Unfortunately they are missing the point. A small randomised trial will give you an estimate that is closer to the truth, because baseline differences are balanced, but the results may be imprecise (wide confidence interval) that is progressively narrowed by increasing the sample size.

However, a large observational study may give you a very precise estimate, but it may be far from the truth (influenced by bias arising from differences in the groups compared), that can never be corrected by increasing the sample size.

Precision of the estimate is never more important than a correct estimate!

The researchers use propensity score adjustment to adjust for differences in measured covariates. There are 3 main ways where propensity score can be used to `balance’ measured differences. The most common is using the propensity score to derive a one-to-one match and discarding any unmatched patients before comparing the two grous. The next is to divide the group into 5 ranges of propensity score and compare them within each range and finally, to include the propensity score as a covariate (which is what was used in this paper) that allows the estimates to be balanced for the measured differences.

All well and good. Unfortunately, the problem does not lie in the propensity score matching of measured variables; it is the unmeasured and unknown variables. For example if institutions that used aprotinin in high risk patients also had a very tight policy on postoperative fluid restriction that predisposed patients to renal impairment independent of the aprotinin.

Statistics can prove association but not causation. A good point made in this study, is the demonstration of a dose response to aprotonin that may be suggestive of causation, but a strong argument can only arise from a series of (previous or future) randomised trials.

Whilst I would love nothing more than to support any cause that would lead to more work for the specialty, I think there is more to the debate.

Wouldn’t it be really unethical to randomize patients with coronary disease anatomy that are already known to derive a survival benefit from CABG to receive PCI? Also, there is no onus to prove that CABG is superior. As far as I can see, the PCI trials ask a different question: `in patients who are amenable to both form of treatment, is there any difference in the outcome between PCI and CABG?’. The trials mainly have the same message, which is lower re-intervention with CABG and no difference in survival. An interesting exception is the SOS trial, where survival was statistically significantly improved with CABG, but the result was glossed over by the reporting authors ("The apparent reduction in mortality with CABG requires further investigation").

We will never stand a fair chance in any revascularization war.

The golden opportunity missed by a generation of cardiac surgeons to take over diagnostic angiography from radiologists, was a move that subsequently led cardiologists to percutaneous coronary intervention. I am sure that surgeons would have superior dexterity and manual skills, if only we had a little more interest and foresight.

Almost invariably, the principal investigators of clinical trials of comparing the two modes of revascularization are cardiologists. Therefore much of the reporting (like the SOS trial) and interpretation of the clinical trial results are performed by cardiologists. Perhaps we need to take the lead in future trials.

The final nail in the coffin must be patient choice. Even if all the facts are presented to the patient fairly, how many would prefer open heart surgery to a less invasive temporizing procedure? Be honest!

I don’t think I’m writing anything that is not already known by all of us. With personal, departmental, financial interests that accompany the revascularization workload and cardiologists sitting at the helm of research, diagnostic investigation and gate keeping, all that is left for people like me to do is to write lamenting articles like this!

Using a `mistletoe test’ (well, the baseline investigation they chose was not that well known either!) you achieved a sensitivity of 15% (95% CI 10 to 23%), and the new `red-nose reindeer’ test achieved a sensitivity of 49% (95% CI 45 to 55%). They concluded that the `red-nose reindeer’ test was at least 3 times more sensitive and should considered for routine diagnosis of `Christmas pudding embolism’.

Problem? Yes… a misconception that invalidates their conclusion.

So how do you interpret a test result that has a sensitivity of 15% and a relatively narrow confidence interval?

Here comes the `science’ bits….

Unlike the usual interpretation, where in a test with high sensitivity, a negative result effectively rules out disease a `low’ sensitivity (i.e. way below 50%) has the interpretation that a negative result effectively rules in disease (ie a negative mistletoe test is a great way to diagnose `Christmas pudding embolism’). In practice, it is never used as such, but more likely to reflect the inappropriateness of the `mistletoe test’.

I guess the bottom line is no matter how confident you are about your research, it’s always a good idea to get a statistician to look through your work prior to submission.

I think off-pump surgery is between phase 1 and 2 of the `Johnson chronology’. What really amuses me is how evangelical surgeons can be when defending their preferred technique. The sentiments are best reflected in this great quote:

`To cut things short, it is extremely important to understand that there is abundant clinically relevant though not necessarily statistically significant, scientific evidence to validate the midterm safety and efficacy of OPCAB.’ Anesthesiology 2005; 103: 902.

Frankly, surgical research can never be 100% replicable and reporting can never be 100% free from bias. The variances in patient response to a tablet (due to pharmacokinetics, pharmacodynamics differences) are usually balanced out if a trial is large enough, but no two surgeons will operate with the same skill. A new procedure that is shown to be superior compared to the standard in the hands of gifted surgeon A, may be inferior to the standard in two-left-hands surgeon B.

Therefore, how much of what can we believe about anything has been reported about off-pump surgery, except for our own intrepretation on the applicability of the raw results of the (randomized) clinical trials?

Cardiothoracic surgery must be the single specialty where the use of statistics is most advanced. Just open any page in Kirklin's and you will be accosted by the most impressive series of numbers, equations and diagrams. Have you ever seen a comparable book in any other medical specialty? To be honest, I’ve always thought that you need a Masters in Statistics to fully comprehend it. It’s exactly what I obtained, and today I think it’s truer than ever.

What hope is there for the standard reader to understand the masses of information presented? The disability leads to a major vulnerability - when you cannot interpret the raw data, you become critically reliant other peoples interpretations.

I always knew there was a good reason to be critically reliant other peoples interpretations.