Earlier this year, delegates of the European Federation of Periodontology (EFP) and the International Diabetes Federation (IDF) had met in Madrid for a joint workshop on an update of the Perio-Diabetes link. I had reported on the event and some key findings, quickly posted on the EFP web page, here.
Already on and after 24 August 2017, a Consensus Report by the two organizations was prematurely published, and quickly (temporarily) withdrawn, in the EFP’s Journal of Clinical Periodontology and the IDF’s Diabetes Research and Clinical Practice. I had managed to get a print-out of the not-yet edited (and later withdrawn) draft version published on the JCP Accepted Articles page and had noticed that most of the evidence presented was derived of yet-to-be published review articles based on the workshop proceedings.
The final version of the Consensus Report (Sanz et al. 2017, Early View Articles), including guidelines for patients and health professionals dealing with patients suffering from diabetes and periodontal disease, went online this week, but still references to review papers presented on the occasion of the workshop have a 2017 assignment and are not paginated which may make it more difficult for scientists and clinicians outside periodontology or dentistry to locate the final papers.
To be clear, when it comes to keeping our medical collegues, and in particular diabetologists, interested in the very long-known link between periodontitis and metabolic diseases, proving beneficial effects of periodontal treatment on diabetic control is crucial. All was fine as long as numerous published, small-scale, mostly single-center, and often poorly executed, trials apparently showed that thorough subgingival scaling in patients with both periodontitis and diabetes led to an about 0.4% reduction of glycated hemoglobin (HbA1c), at least after three or four months. As that would in effect spare an additional antidiabetic drug, diabetologists stayed interested. Although results in a few trials indicated that the effect was not long-lasting, i.e., no longer discernable after, say, six months.
The recent largely expanded Cochrane Systematic Review on periodontal treatment for glycemic control in diabetics by Simpson et al. 2015 calculates, in one of numerous meta-analyses, a weighted mean 0.29% reduction (95% confidence interval 0.10% lower to 0.48% lower) of HbA1c 3-4 months after nonsurgical periodontal therapy. Fourteen clinical trials were considered comprising about 1499 patients with both diabetes and periodontitis. The quality of evidence was considered low. Quality was downgraded twice, first for risk of bias, mainly due to lack of blinding; and then due to moderate heterogeneity (I2 = 0.53%). The observed small reduction of 0.29% was not sustained afterwards . At 6-month follow-up (the meta-analysis considered 5 studies with 826 patients), the weighted mean reduction was 0.02% (95% CI 0.20% lower to 0.16% higher).
Yesterday, new NHANES 2009-2012 data on prevalence, extent and severity of periodontitis have gone online in the Journal of Periodontology. On first sight, authors confirm findings of the previous, 2009-2010, survey in that prevalence is much larger as previously reported. So, 46% of U.S. adults have periodontitis with almost 9% having severe disease (Eke et al. 2015). The previous report (Eke et al. 2012a) contained an unclear description of how attachment loss was measured concealing that a “signed” measure of recession was used to calculate clinical attachment loss as difference of probing pocket depth and recession (from Latin, recessus, retreat). In a letter to the Editor-in-Chief of the Journal of Dental Research, Professor Giannobile, I had raised more problems in the article when I wrote,
“Teaching in particular undergraduates about how probing parameters periodontal probing depth, attachment level, and recession are measured is quite an effort but usually straightforward. In order to avoid undue exaggeration of prevalence, extent and severity of periodontitis both in the population and in patients attending a common office and to be able to assess treatment outcomes, metric periodontal probing parameters have to be properly defined. I would therefore appreciate if authors could comment on the apparent redefinition of attachment loss in their paper. When analyzing the Figure in the paper by Eke et al. (2012a), what immediately hits the eye is that there seems to be higher prevalence of attachment loss at different thresholds (a) than of pocket depth at respective thresholds (b) in all age groups. Such a pattern may actually be a result of how attachment loss had erroneously been redefined, most probably due to convenience. Just as a trivial example, a 4 mm probing depth without recession may be associated with either 0, 1, 2, 3, or 4 mm attachment loss, but the NHANES oral health data management program would have “instantly calculated” 4 mm. Based on the new case definition using attachment loss in addition to probing depth, prevalence of all periodontitis in the adult population of 30 years and older in the U.S. has now been estimated to exceed 47%, after 35% found in NHANES III during 1988-1994. This much higher prevalence may be due to the redefinition of attachment loss, too. Moreover, as to Eke et al. (2012a), mild periodontitis has a rather low prevalence in all age groups while moderate periodontitis is widespread (Figure c). The picture was different in NHANES III when severe periodontitis occurred with lowest, moderate periodontitis with intermediate and mild periodontitis with highest prevalence, a pattern which, I suppose, applies to many other widespread chronic diseases. The strange new pattern might indeed be explained partly by the redefinition of attachment loss as well, ultimately leading to a different distribution of cases.” (Emphasis added.)
Subtracting recession from periodontal probing depth makes sense only when true recession (the free gingival margin is located apical to the cemento-enamel junction) gets a minus sign. This was circumstantially explained to me in an email by the authors forwarded to me by Professor Giannobile, who never published my original letter. Eke et al. (2012a) had actually concealed that a signed recession definition was used. In the new update of NHANES 2009-2012, calculation of clinical attachment is now correctly described, including the signed recession definition. Eke et al. (2015) may also have realized that there is no complex chronic disease where moderate severity is more prevalent than its mild form. It is rather perplexing to see that authors have now abandoned the differentiation between moderate and mild periodontitis which they call “other” periodontitis (other than severe). They give the following reason,
“These subgroups [mild and moderate periodontitis] are not truly ordinal [sic] as the label suggests because many ‘moderate’ cases had insufficient pocket depth to qualify as ‘mild’ and we have therefore combined them and used the label ‘other‘ periodontitis.”
The unpleasant taste may prevent the normal population from using diluted bleach as a mouthwash. A recent pilot study, which has resulted already in two papers (since pooled microbiological samples had been taken, one might expect at least another paper) in the once prestigious Journal of Periodontal Research, might leave scientists even more skeptical. The published RCT does not mention the CONSORT statement. Apparently, no sample size was calculated. Randomization took place and 15 test patients with untreated periodontitis were asked to rinse twice per week with 0.25% sodium hypochlorite while 15 patients were supposed to rinse twice per week with water [sic] for 3 months. At baseline and after 2 weeks, patients received oral hygiene instructions, and pockets were irrigated with either 0.25% sodium hypochlorite or, well, water. The test solution was prepared by the patients, one teaspoonful Chlorox (6% sodium hypochlorite) on one-half glass of water (5 mL on 120 mL).
It is very much concerning that just 12 out of 30 patients (40%) completed the 3-month trial. While awful taste of Chlorox was actually mentioned by two patients who, for that, missed couple of rinses, according to Galvan et al. concerns of delay of proper periodontal treatment and transportation issues were the main reasons for drop outs.
But what is even more disturbing is how the authors analyzed their data. Although Galvan et al. (2014) claim that the subject was the unit for all statistical analyses, Gonzales et al., in an additional analysis of just 7 test and 5 control subjects who completed the 3-month trial write,
“The individual pockets were treated as independent statistical units, based on nonspecific and wide-ranging antimicrobial action of sodium hypochlorite and the observation that pockets with a large range of depths responded positively to the bleach treatment and that residual bleeding on probing sites showed no tendency to cluster in particular patients or around specific teeth.” (Emphasis added.)
Most of spurious evidence of the 1970s and 1980s in periodontics stems from that misconception, be it clinical responses when pockets with different depths were considered independent in a limited number of patients, or observations made in microbiological samples from numerous sites in certain patients. At least since Larry L. Laster’s paper of 1985, periodontists must be aware of inflated p-values and spurious conclusions.
The first withdrawn manuscript by Drs. Wenche Borgnakke and Iain Chapple and each and every editor of our hardcore periodontal journals as well as otherwise eminent individual in Periodontology, which had proclaimed that “[t]he randomized controlled trial (RCT) published by the Journal of the American Medical Association (JAMA) on the impact of periodontal therapy on glycated hemoglobin (HbA1c) has fundamental flaws” about the paper by Engebretson et al. (2013), see [pdf], went online today in the Journal of Evidence-Based Dental Practice.
I had wondered before why it had been withdrawn but couldn’t figure that out. Interesting may be that the withdrawn paper had listed all 19 authors, while the current version does not. Maybe that Borgnakke and Chapple are only pawns in a worldwide political enterprise launched by our “thought leaders”. It may also be that more “evidence” (see below), possibly (but rather not) suitable for putting findings by Engebretson et al. (2013) into perspectve, needed to be included in what is almost a revile.