Dear Editor,

The authors correctly point out that their proposed modification will require revalidation of the criteria and, like Olivieri and Spadaro, I agree that the criteria will need to be revisited for early disease.
However, for now they are the best we have and they should be used for epidemiology and clinical trials. I am puzzled how the Moll and Wright criteria performed better than CASPAR, since the M+W criteria are nested within the CASPAR criteria - perhaps the authors (unintenionally) modified M+W by including a documented past history of psoriasis as the stem.

Dear Editor,

We appreciated the efforts by the EUSTAR committee to provide recommendations for endothelial progenitor cell (EPC) analyses. We agree that EPC methods should be uniformed, as considerable disagreement exist that is likely to limit research advancement.[1] However, the piece contains some statements that might lead to a misinterpretation of future data on EPC analyses. These aspects have been previously reported by our group in a recent methodological review.[2]
The existence of different subpopulations of EPCs, as described in the paper, refers only to cultured EPCs. In this regards, we agree that “early” short-term cultured EPCs are mainly CD14-positive (so-called monocytic EPCs), while “late” outgrown EPCs are mainly CD14-negative (so- called true EPCs). However, there is no correlation or identity between cultured cells and the antigenic phenotype of ex vivo FACS-determined EPCs. Indeed, most plated cells are originally CD14-positive and culture conditions can induce downregulation of CD14, in parallel with upregulation of endothelial markers and genes. A similar behaviour ha been reported for the panleukocyte antigen CD45 [3]. Clearly pre-plating is the step responsible for yielding monocytic EPCs, which are monocytes/macrophages assuming an endothelial-like phenotype in culture.[4] Moreover, it should be noted that no single coating strategy has shown superiority over the others, but most protocols used fibronectin as the preferential substrate for endothelial cell growth.[2] We feel that the most important recommendation regarding EPC culture should be to avoid the use of the short-term colony forming unit-endothelial cells (CFU-EC), which simply force monocytes and lymphocytes to differentiate into spurious endothelial cells with no true transdifferentiation, as shown by gene profiling.[5-7]
Another unclear point is that the paper often confuses cultured EPCs and circulating EPCs defined by FACS. We are sure that the authors agree that it is critical that these cells should be kept separated because there is no evidence that the two different methods explore the same biological entity. Thus, there is no evidence supporting the need for depletion of CD14 and/or CD45 expressing cells before FACS analyses for EPC markers.
As shown by Case et al. CD133+CD34+KDR+ cells are likely to be enriched with hematopoietic stem cells rather than EPCs,[8] because the use of the CD133 marker moves away from endothelial biology. That CD133 cells can be differentiated into mature endothelial cells is irrelevant as this is accomplished through downregulation of CD133.[2]. The utility of the suggested procedure of enriching CD34/CD133-positive cells or depleting Lin-positive cells before FACS is far to be demonstrated. In fact, the purer the cell population, the lower the number of events that can be acquired by FACS, and the higher the coefficient of variability (CV) of the measure according to the Poisson distribution for rare events (for a review of these arguments see [2]).
Finally, we would like to comment on an interesting aspect pointed out in figure 2. The figure shows that the use of a viability marker allows to demonstrate that most (if not all) CD34+CD133+KDR+ EPCs are not viable in a representative subject with scleroderma. In our experience not more of 10-15% of immature mononuclear cells are usually not viable. Thus, one could ask whether the staining showed on figure 2a is related to the intrinsic characteristics of the disease or whether the concomitant use of immunosuppressants may influence the analysis. In this case, caution should be advised on the possibility that a non specific staining may influence the enumeration of EPCs.

References

1. Leor J and Marber M. Endothelial progenitors: a new Tower of Babel? J Am Coll Cardiol 2006;48:1588-1590.

2. Fadini GP, Baesso I, Albiero M et al. Technical notes on endothelial progenitor cells: ways to escape from the knowledge plateau. Atherosclerosis 2008;197:496-503.

3. Ingram DA, Caplice NM and Yoder MC. Unresolved questions, changing definitions, and novel paradigms for defining endothelial progenitor cells. Blood 2005;106:1525-1531.

4. Rohde E, Bartmann C, Schallmoser K et al. Immune cells mimic the morphology of endothelial progenitor colonies in vitro. Stem Cells 2007;25:1746-1752.

5. Rohde E, Malischnik C, Thaler D. et al. Blood monocytes mimic endothelial progenitor cells, Stem Cells. 2006;24:357-367.

6. Yoder MC, Mead LE, Prater D et al. Redefining endothelial progenitor cells via clonal analysis and hematopoietic stem/progenitor cell principals. Blood 2007;109:1801-1809.

7. Hur J, Yang HM, Yoon CH et al. Identification of a novel role of T cells in postnatal vasculogenesis: characterization of endothelial progenitor cell colonies. Circulation 2007;116:1671-1682.

8. Case J, Mead LE, Bessler WK et al. Human CD34+AC133+VEGFR-2+ cells are not endothelial progenitor cells but distinct, primitive hematopoietic progenitors. Exp Hematol 2007;35:1109-1118.

Dear editor,

In the Dec 3, 2008 online issue of The Annals, Simon et al did a comparison of the rate of cancers occurring in the rheumatoid arthritis (RA) abatacept clinical development program with malignancies occurring in five observational RA cohorts (1). The main result of this study is that the rate of cancers in patients included in the clinical trials of abatacept is the same than in RA cohorts.

This type of comparison, presented in figure 1, deserves a major concern. As the authors themselves state, the patients included in the seven abatacept trials were selected, like all patients in trials. For example, in five of these trials mammography was advised before inclusion and patients with suspicious mammography were excluded. In contrast, patients included in RA cohorts are not selected patients.

The selection of patients with a low risk of cancer in RA clinical trials has been well demonstrated in the placebo groups of randomized clinical trials with anti TNF therapy. In the meta-analysis by Bongartz et al. of randomized clinical trials with infliximab and adalimumab, the rate of cancers in the placebo groups was eight times lower than expected in the general population of same age and sex (2, 3). In a meta-analysis of randomized control trials of infliximab performed by the US food and drug administration, the rate of cancers was five times lower in the placebo groups than expected in the general population of same age and sex (4).

Therefore, the only valid comparison is the comparison of the rate of cancer between abatacept-treated patients and placebo-treated patients in the randomized control trials. The authors did this comparison and did not find any difference. Even with the limitation of a much lower number of patients in the placebo groups (989 patients and 794 patients-years versus 4134 patients and 8388 patient-years in the abatacept groups), this result is the most important of the study and should be emphasized instead of the comparison with the patients included in cohorts.

Number of registries all over the world include patients treated with abatacept, some of them dedicated to patients treated with this drug and, in the next future, it will be possible to compare the rate of cancers occurring in these patients in comparison with other RA patients included in cohorts.

References

1. Simon TA, Smitten AL, Franklin J, Askling J, Lacaille D, Wolfe F, et al. Malignancies in the rheumatoid arthritis abatacept clinical development program: An epidemiological assessment. Ann Rheum Dis 2008 Dec 3 [Epub ahead of print].

2. Bongartz T, Sutton AJ, Sweeting MJ, Buchan I, Matteson EL, Montori V. Anti-TNF antibody therapy in rheumatoid arthritis and the risk of serious infections and malignancies: systematic review and meta-analysis of rare harmful effects in randomized controlled trials. Jama 2006;295:2275-2285.

3. Dixon W, Silman A. Is there an association between anti-TNF monoclonal antibody therapy in rheumatoid arthritis and risk of malignancy and serious infection? Commentary on the meta-analysis by Bongartz et al. Arthritis Res Ther 2006;8:111.

4. Okada SK, Siegel JN. Risk of serious infections and malignancies with anti-TNF antibody therapy in rheumatoid arthritis. Jama 2006;296:2201-2.

Dear editor,

We read with interest 'A randomised controlled trial of spinal manipulative therapy in acute back pain' by Peter Jüni, Markus Battaglia, Eveline Nüesch et al. in Annals of the Rheumatic Diseases (online 5 Sept, 2008). We congratulate the authors on their attempt to investigate the effectiveness of spinal manipulative therapy (SMT) in the routine clinical practice setting. We also congratulate the authors for their meticulous attention to detail in various parts of their methodology, particularly to reduce bias through randomization, in-tention-to-treat analysis and control and monitoring of co-interventions.

However, we wish to raise some methodological and theoretical concerns regarding the ability of this study to answer the research question as to whether SMT in addition to standard medical treatment is associated with clinically relevant early reductions in pain and analgesic consumption.

Sufficient power is a critical part of the randomised controlled trial (RCT). Jüni et al. calculated that 51 patients per group were needed to achieve more than 80% power in their multilevel model to answer their research question. The research question clearly states that SMT is the treatment being investigated. Unfortunately as described in the methods, spinal mobilization and muscle energy (ME) techniques were also employed at the discre-tion of the treating clinician. The result was that only 38 out of the 52 experimental group participants (73%) actually received SMT in an 'estimated' 80% of the treatment sessions. It is not made clear what the other 37% of SMT group participants received. The unmistakeable bottom line is that this study is underpowered and therefore unable to answer its primary research question. We respectfully ask how the authors can justify their conclusions that SMT is unlikely to result in early pain reductions in acute low back pain patients using an underpowered study?

We have two major concerns regarding recruitment. Firstly, we are unclear as to the reason for using an Emergency Department in combination with a private medical care prac-tice for patient recruitment. The types of patients encountered in an Emergency Ward are unlikely to be typical of acute back pain patients found in routine clinical practice. Therefore we question how applicable are these participants for this study? We are unsure of the methodological rationale for using two such diverse clinical settings.

Secondly, and following on from the issue of recruitment sites, we are also concerned that it took more than 3 years to recruit the 104 acute low back pain patients. We assume that the purpose of this study was to look at the benefit of SMT in the typical clinical setting. As recruitment time lengthens to achieve the sample size estimate, so also do the questions about how representative are the participants to routine clinical practice? Both of these recruitment issues raise further concerns about the ability of this study to answer its fundamental research question.

Another concern is the comparability of the experimental and control groups at baseline as identified in Table 1. An assessment of these groups shows that the experimental (Standard Care & SMT) showed considerably greater duration of pain complaint compared to the Standard Care control group (46% versus 25% >/= 7 days); greater pain intensity (BS 11 score >/= 7: 58% versus 48%) yet were more fully able to work (53% versus 37%), and took less medication (116 versus 131 Diclofenac equivalence dose).

Taken together the experimental group typically had more pain for longer, were likely still working and were less inclined to take medication. It is well known that psychosocial variables are important factors for back pain. These differences at baseline are likely to have influenced the final results of this study. It is unfortunate that no psychosocial variables were investigated as some of these may have been important in terms of baseline characteristics to help explain some of the observed differences. As such, the differences in these baseline characteristics are likely to have impacted on the overall results of this study in meaningful ways that cannot be explained by the present study.

Finally, we suggest that most clinicians and researchers in the field of back pain would agree that the current categorization of mechanical/simple low back pain is insufficient. There are likely a number of subgroups that make up what we currently call low back pain of mechanical origin. We respectfully suggest that the current focus of research for low back and neck pain should be two-fold. First, the identification of subgroups and their defining characteristics is paramount. Second, we suggest that back and neck pain are functional conditions that need appropriate functional outcome measures for their as-sessment. Therefore we suggest that the second focus should be on the development and psychometric testing of new functional outcome measures that are valid, reliable and sensitive for use in mechanical low back and neck pain subgroups.

Until we have identified subgroups and can measure their defining characteristics, further studies using the Randomized Controlled Trial methodology does not appear to be rational for low back and neck pain research. We sincerely hope that the authors would join us in our efforts to address these two important issues.