How It All Began

in-the-court-of-the-crimson-king

Readers may have noticed my dismay about our “thought leaders'” recent attempts to revive the perio/systemic issue despite emerging evidence of no or very small, irrelevant, effects of periodontal treatment in large-scale intervention studies on  HbA1c in type 2 diabetes, or pregnancy outcomes.

I had yesterday discussed via email with a critical mind in the U.S. the results of another intervention study on cardiovascular events which never made it beyond a pilot study, the Periodontitis and Vascular Events, or PAVE, study. Since periodontitis patients were not randomized according to whether they received periodontal treatment but according to a community comparator (referral to community dentist with copy of x-rays and letter with diagnosis and recomendations for treatment), I had argued that such a design would not fulfil criteria of an RCT since patients who get proper periodontal treatment in the comparison group may fundamentally differ from those who won’t care. However, patients who won’t care in the test group would get the treatment anyway. So, interpretation of biased results would be difficult if impossible. Not surprising, the PAVE study did not get funding after the pilot phase (Beck et al. 2009) [pdf], which resulted in non-significant differences anyway, possibly (but not inevitably) due to lack of statistical power.

I remember that I had been confused if not appalled when the same group of scientists had criticized, in a letter to the editors of JAMA, the conclusions drawn in a data-mining study by Hujoel et al. (2000) [pdf]. Dr. Hujoel and coworkers at the University of Washington in Seattle had used the huge database of the U.S. population-based first National Health and Nutrition Examination Survey (NHANES I) of 1971-1975 and its epidemiologic  follow-up (1982-1984, 1986, 1987, and 1992) of participants between 25 and 74 yr of age. They evaluated three periodontal conditions at baseline (periodontitis, gingivitis and periodontal health) and the incidence of the first subsequent coronary heart disease (CHD) event observed.  Hujoel et al. (2000) had found that, after thorough adjustment for known and potential confounders, hazard ratios for CHD events associated with periodontitis and gingivitis were 1.14 (95% CI 0.96-1.36) and 1.05 (0.88-1.26), respectively, while hazard rations for CHD fatalities were 1.20 (0.90-1.61) and 1.17 (0.84-1.61), respectively. They did further dose-response analyses and determined the risk for subjects with different numbers of teeth at baseline, different severity of periodontal disease, different age groups and different degrees of inflammation. Hujoel et al. concluded that,

The results of this study do not provide convincing evidence that periodontitis and gingivitis are associated with CHD. Gingivitis was not associated with CHD. Periodontitis was associated with a non-significant increased risk for CHD.

“While this study did provide convincing evidence regarding absence of a moderate-to-large association between periodontitis and CHD, a small causal association could not be ruled out. (My emphasis.)

Apart from periodontal disease case definitions in 1971-1975 being crude (periodontitis and gingivitis were diagnosed by applying Russell’s Periodontal Index of 1956, a citation classic in 1979), the paper by Hujoel et al. and in particular its statistical analysis (no wonder, three of the authors were renowned biostatisticians and epidemiologists) including careful conclusions were sound. The paper was published on 20 September 2000.

On 3 January 2001, a letter to the editors by Drs. Robert J. Genco, Maurizio Trevisan, Tiejian Wu at SUNY, Buffalo; and James Beck, University of North Carolina at Chapel Hill appeared in JAMA, where they point to “several limitations in the NHANES I data [that] may limit the apparent association between PD [periodontal disease] and CHD.” They “believe that their [Hujoel et al.] conclusion about lack of an association between PD and CHD is premature and unsubstantiated.”

First, the measure of periodontal disease in NHANES I is subjective and less accurate than objective measures like those used in NHANES III. Hence, misclassification of PD is likely. A longitudinal study [reference to Beck et al. 1996] that used an objective measure of PD showed a strong association between PD and CHD in men.

A further limitation is that PD was measured at baseline only, and changes in periodontal status during the 20-year follow-up in periodontal were not taken into account. Some of those who had no PD at baseline would be expected to develop the disease later because the prevalence of PD increases markedly with age. Also, the extent of PD in those who already had PD may have been reduced by treatment. Because there are no available data that measure changes over time in periodontal status, the association between PD and CHD might be biased toward the null hypothesis. This issue becomes more problematic as the length of follow-up increases.

Finally, many of the pathophysiological mechanisms that have been hypothesized as links between PD and CHD relate to the triggering of clinical coronary events [reference to Herzberg et al. 1994]. These triggering factors are most significant when they occur close in time to the clinical outcomes; therefore, longitudinal studies may not represent the best study design to investigate these associations.

Drs. Philippe P. Hujoel, Mark T. Drangsholt, C. Spiekerman, and Timothy A. DeRouen replied to each issue raised,

Misclassification bias: Genco et al describe our PD measures as “subjective and less accurate” than the objective measures used, for instance, by Beck et al,1 who showed a “strong association.” However, in a field beset by lack of a standard definition of periodontitis, there is no evidence that our surrogate markers are less accurate or more subjective in measuring PD than the surrogate markers used in studies with positive findings [reference to Hujoel and DeRouen 1988]. Furthermore, the odds ratio of 1.5 in the study by Beck et al does not represent a strong association, especially since it was not adjusted for smoking.

Changes in periodontal status during follow-up: While it would be desirable to include longitudinal data on periodontal status, such data are not available. In our study, we investigated whether the estimates of periodontitis-associated CHD hazard changed during the follow-up. No convincing evidence was found (P=.13).

Other studies: The 3 largest studies done to date, including our study, reported the CHD relative risks shown in the TABLE [including a meta-analysis]. The summary relative risk of 1.07, a consistent conclusion of no association across 3 populations, the presence of both short-term and long-term follow-up (addressing the issue of possible dilution effects), the use of different periodontitis measures, and detailed control for confounding variables all argue against a moderate-to-strong association between PD and CHD.

The above mentioned TABLE summarized the results of the study by Hujoel et al. (2000), the Health Professional Follow-up Study by  Joshipura et al. (1996) and the US Physicians’ Health Study by Christen et al. (1998) which had been published as an abstract in the journal Circulation only. The meta-analysis considered more than 74,000 subjects with follow-up between less than 6 and 16.1 yr on average with more than 2800 CHD events. The relative risk was 1.07 with a 95% confidence interval of 0.96-1.19.

In their critique, Genco et al. (2001) did not mention that their group had just published their own paper on periodontal disease and cerebrovascular accidents (CVA) which exploited the same data set as Hujoel et al., NHANES I and its epidemiologic follow-up. The paper by Wu et al. (2000) [pdf] had appeared on 9 October 2000 in Archives of Internal Medicine (now merged with JAMA), 19 days after that by Hujoel et al. (2000). It was, what we then called, in print. It had been accepted for publication 4 May 2000.

The material (subjects, crude periodontal examination, long follow-up)  was the same, so how about case definitions? Hujoel et al. classified 1859 subject as having periodontitis, 2421 as having gingivitis and 3752 as periodontally healthy (8032 in total). Wu et al. (2000) classified 1800 as periodontitis subjects, 2346 as gingivitis subjects, 3634 as having no disease (7780). Two thousand eighty-two were edentulous which were excluded by Hujoel et al. Wu et al. (2000) found that,

[c]ompared with no periodontal disease, the relative risks (95% confidence intervals) for incident nonhemorrhagic stroke were 1.24 (0.74-2.08) for gingivitis, 2.11 (1.30-3.42) for periodontitis, and 1.41 (0.96-2.06) for edentulousness. For total CVA, the results were 1.02 (0.70-1.48) for gingivitis, 1.66 (1.14-2.39) for periodontitis, and 1.23 (0.91-1.66) for edentulousness.

Wu et al. concluded that “this prospective study suggests that periodontitis is significantly associated with risk of developing CVA and, in particular, nonhemorrhagic stroke.” Not only the same concerns expressed when considering the paper by Hujoel et al. (2000) would apply here: misclassification and changes in periodontal status during follow-up. They even dealt with the same material.

So, if and when a moderate association of periodontitis with cardiovascular or cerebrovascular disease can be found, it seems to be irrelevant whether the study has design or methodological problems (NHANES I and its epidemiologic follow-up certainly has). However, if and when the analyis yields no association, it must be due to problems with design and methods. Has that hypocrisy been overlooked in the scientific community?

Similar, agitated, disputes could later be noted when a large intervention study by Michalowicz et al. (2006) [pdf] did not yield a significant effect on pregnancy outcomes (which had later to be confirmed by Offenbacher et al. (2009) [pdf]  in a twice as large intervention trial), last year when Lockhart et al. (2012) [pdf], in an exhaustive systematic review, concluded that there is currently no evidence that periodontal interventions prevent atherosclerotic vascular disease or modify its outcomes; and the other day, when Engebretson et al. (2013) [pdf]  found, in a large intervention study, no effect of basic periodontal treatment (i.e., nonsurgical) on HbA1c levels in type 2 diabetic patients.

A recent development has been that workshops are organized by our specialty organizations AAP and EFP to fix unwelcome results of large intervention studies by creating new systematic reviews.  It can be assumed that independent peer review is not granted in that case. In addition, apart from supersaturation (which ultimately leads to ignorance among the medical profession rather than respect for our specialty), the usually complicated message is frequently boiled down into an easy to digest “manifesto” or youtube video which may mislead the obvious target, the busy practitioner.

There has recently been a surge of  systematic reviews  which are frequently just repeating what we know already. If new and large intervention studies are submitted, editors should demand the systematic review of previous studies included and, if possible, a meta-analysis. As a rule, new high quality RCTs should be larger than (may be twice as) the largest previous study in order to challenge the results of the former meta-analysis. In the presence or anticipation of intervention studies, new systematic reviews of observational studies (especially case-control but even cohort studies, e.g. Dietrich et al. (2013) [pdf]) which have shown weak or moderate associations between, e.g., periodontal disease and cardiovascular events in the presence of confounding won’t make too much sense. They cannot prove causality anyway.

30 December 2013 @ 5:55 pm.

Last modified January 16, 2014.

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