Sugary Drinks as the Culprit in Childhood Obesity? a RCT among Primary School Children

24 09 2012

ResearchBlogging.org Childhood obesity is a growing health problem. Since 1980, the proportion of overweighted children has almost tripled in the USA:  nowadays approximately 17% of children and adolescents are obese.  (Source: cdc.gov [6])

Common sense tells me that obesity is the result of too high calory intake without sufficient physical activity.” - which is just what the CDC states. I’m not surprised that the CDC also mentions the greater availability of high-energy-dense foods and sugary drinks at home and at school as main reasons for the increased intake of calories among children.

In my teens I already realized that sugar in sodas were just “empty calories” and I replaced tonic and cola by low calory  Rivella (and omitted sugar from tea). When my children were young I urged the day care to restrain from routinely giving lemonade (often in vain).

I was therefore a bit surprised to notice all the fuss in the Dutch newspapers [NRC] [7] about a new Dutch study [1] showing that sugary drinks contributed to obesity. My first reaction was “Duhhh?!…. so what?”.

Also, it bothered me that the researchers had performed a RCT (randomized controlled trial) in kids giving one half of them sugar-sweetened drinks and the other half sugar-free drinks. “Is it ethical to perform such a scientific “experiment” in healthy kids?”, I wondered, “giving more than 300 kids 14 kilo sugar over 18 months, without them knowing it?”

But reading the newspaper and the actual paper[1], I found that the study was very well thought out. Also ethically.

It is true that the association between sodas and weight gain has been shown before. But these studies were either observational studies, where one cannot look at the effect of sodas in isolation (kids who drink a lot of sodas often eat more junk food and watch more television: so these other life style aspects may be the real culprit) or inconclusive RCT’s (i.e. because of low sample size). Weak studies and inconclusive evidence will not convince policy makers, organizations and beverage companies (nor schools) to take action.

As explained previously in The Best Study Design… For Dummies [8] the best way to test whether an intervention has a health effect is to do a  double blind RCT, where the intervention (in this case: sugary drinks) is compared to a control (drinks with artificial sweetener instead of sugar) and where the study participants, and direct researchers do not now who receives the  actual intervention and who the phony one.

The study of Katan and his group[1] was a large, double blinded RCT with a long follow-up (18 months). The researchers recruited 641 normal-weight schoolchildren from 8 primary schools.

Importantly, only children were included in the study that normally drank sugared drinks at school (see announcement in Dutch). Thus participation in the trial only meant that half of the children received less sugar during the study-period. The researchers would have preferred drinking water as a control, but to ensure that the sugar-free and sugar-containing drinks tasted and looked essentially the same they used an artificial sweetener as a control.

The children drank 8 ounces (250 ml) of a 104-calorie sugar-sweetened or no-calorie sugar-free fruit-flavoured drink every day during 18 months.  Compliance was good as children who drank the artificially sweetened beverages had the expected level of urinary sucralose (sweetener).

At the end of the study the kids in the sugar-free group gained a kilo less weight than their peers. They also had a significant lower BMI-increase and gained less body fat.

Thus, according to Katan in the Dutch newspaper NRC[7], “it is time to get rid of the beverage vending machines”. (see NRC [6]).

But does this research really support that conclusion and does it, as some headlines state [9]: “powerfully strengthen the case against soda and other sugary drinks as culprits in the obesity epidemic?”

Rereading the paper I wondered as to the reasons why this study was performed.

If the trial was meant to find out whether putting children on artificially sweetened beverages (instead of sugary drinks) would lead to less fat gain, then why didn’t the researchers do an  intention to treat (ITT) analysis? In an ITT analysis trial participants are compared–in terms of their final results–within the groups to which they were initially randomized. This permits the pragmatic evaluation of the benefit of a treatment policy.
Suppose there were more dropouts in the intervention group, that might indicate that people had a reason not to adhere to the treatment. Indeed there were many dropouts overall: 26% of the children had stopped consuming the drinks, 29% from the sugar-free group, and 22% from the sugar group.
Interestingly, the majority of the children who stopped drinking the cans because they no longer liked the drink (68/94 versus 45/70 dropouts in the sugar-free versus the sugar group).
Ànd children who correctly assumed that the sweetened drinks were “artificially sweetened” was 21% higher than expected by chance (correct identification was 3% lower in the sugar group).
Did some children stop using the non-sugary drinks because they found the taste less nice than usual or artificial? Perhaps.

This  might indicate that replacing sugar-drinks by artificially sweetened drinks might not be as effective in “practice”.

Indeed most of the effect on the main outcome, the differences in BMI-Z score (the number of standard deviations by which a child differs from the mean in the Netherland for his or her age or sex) was “strongest” after 6 months and faded after 12 months.

Mind you, the researchers did neatly correct for the missing data by multiple imputation. As long as the children participated in the study, their changes in body weight and fat paralleled those of children who finished the study. However, the positive effect of the earlier use of non-sugary drinks faded in children who went back to drinking sugary drinks. This is not unexpected, but it underlines the point I raised above: the effect may be less drastic in the “real world”.

Another (smaller) RCT, published in the same issue of the NEJM [2](editorial in[4]), aimed to test the effect of an intervention to cut the intake of sugary drinks in obese adolescents. The intervention (home deliveries of bottled water and diet drinks for one year) led to a significant reduction in mean BMI (body mass index), but not in percentage body fat, especially in Hispanic adolescents. However at one year follow up (thus one year after the intervention had stopped) the differences between the groups evaporated again.

But perhaps the trial was “just” meant as a biological-fysiological experiment, as Hans van Maanen suggested in his critical response in de Volkskrant[10].

Indeed, the data actually show that sugar in drinks can lead to a greater increase in obesity-related parameters (and vice versa). [avoiding the endless fructose-glucose debate [11].

In the media, Katan stresses the mechanistic aspects too. He claims that children who drank the sweetened drinks, didn’t compensate for the lower intake of sugars by eating more. In the NY-times he is cited as follows[12]: “When you change the intake of liquid calories, you don’t get the effect that you get when you skip breakfast and then compensate with a larger lunch…”

This seems a logic explanation, but I can’t find any substatation in the article.

Still “food intake of the children at lunch time, shortly after the morning break when the children have consumed the study drinks”, was a secondary outcome in the original protocol!! (see the nice comparison of the two most disparate descriptions of the trial design at clinicaltrials.gov [5], partly shown in the figure below).

“Energy intake during lunchtime” was later replaced by a “sensory evaluation” (with questions like: “How satiated do you feel?”). The results, however were not reported in their current paper. That is also true for a questionnaire about dental health.

Looking at the two protocol versions I saw other striking differences. At 2009_05_28, the primary outcomes of the study are the children’s body weight (BMI z-score),waist circumference (replaced by waist to height), skin folds and bioelectrical impedance.
The latter three become secondary outcomes in the final draft. Why?

Click to enlarge (source Clinicaltrials.gov [5])

It is funny that although the main outcome is the BMI z score, the authors mainly discuss the effects on body weight and body fat in the media (but perhaps this is better understood by the audience).

Furthermore, the effect on weight is less then expected: 1 kilo instead of 2,3 kilo. And only a part is accounted for by loss in body fat: -0,55 kilo fat as measured by electrical impedance and -0,35 kilo as measured by changes in skinfold thickness. The standard deviations are enormous.

Look for instance at the primary end point (BMI z score) at 0 and 18 months in both groups. The change in this period is what counts. The difference in change between both groups from baseline is -0,13, with a P value of 0.001.

(data are based on the full cohort, with imputed data, taken from Table 2)

Sugar-free group : 0.06±1.00  [0 Mo]  –> 0.08±0.99 [18 Mo] : change = 0.02±0.41  

Sugar-group: 0.01±1.04  [0 Mo]  –> 0.15±1.06 [18 Mo] : change = 0.15±0.42 

Difference in change from baseline: −0.13 (−0.21 to −0.05) P = 0.001

Looking at these data I’m impressed by the standard deviations (replaced by standard errors in the somewhat nicer looking fig 3). What does a value of 0.01 ±1.04 represent? There is a looooot of variation (even though BMI z is corrected for age and sex). Although no statistical differences were found for baseline values between the groups the “eyeball test” tells me the sugar- group has a slight “advantage”. They seem to start with slightly lower baseline values (overall, except for body weight).

Anyway, the changes are significant….. But significance isn’t identical to relevant.

At a second look the data look less impressive than the media reports.

Another important point, raised by van Maanen[10], is that the children’s weight increases more in this study than in the normal Dutch population. 6-7 kilo instead of 3 kilo.

In conclusion, the study by the group of Katan et al is a large, unique, randomized trial, that looked at the effects of replacement of sugar by artificial sweeteners in drinks consumed by healthy school children. An effect was noticed on several “obesity-related parameters”, but the effects were not large and possibly don’t last after discontinuation of the trial.

It is important that a single factor, the sugar component in beverages is tested in isolation. This shows that sugar itself “does matter”. However, the trial does not show that sugary drinks are the main obesity  factor in childhood (as suggested in some media reports).

It is clear that the investigators feel very engaged, they really want to tackle the childhood obesity problem. But they should separate the scientific findings from common sense.

The cans fabricated for this trial were registered under the trade name Blikkie (Dutch for “Little Can”). This was to make sure that the drinks would never be sold by smart business guys using the slogan: “cans which have scientifically been proven to help to keep your child lean and healthy”.[NRC]

Still soft drink stakeholders may well argue that low calory drinks are just fine and that curbing sodas is not the magic bullet.

But it is a good start, I think.

Photo credits Cola & Obesity:  Melliegrunt Flikr [CC]

  1. de Ruyter JC, Olthof MR, Seidell JC, & Katan MB (2012). A Trial of Sugar-free or Sugar-Sweetened Beverages and Body Weight in Children. The New England journal of medicine PMID: 22998340
  2. Ebbeling CB, Feldman HA, Chomitz VR, Antonelli TA, Gortmaker SL, Osganian SK, & Ludwig DS (2012). A Randomized Trial of Sugar-Sweetened Beverages and Adolescent Body Weight. The New England journal of medicine PMID: 22998339
  3. Qi Q, Chu AY, Kang JH, Jensen MK, Curhan GC, Pasquale LR, Ridker PM, Hunter DJ, Willett WC, Rimm EB, Chasman DI, Hu FB, & Qi L (2012). Sugar-Sweetened Beverages and Genetic Risk of Obesity. The New England journal of medicine PMID: 22998338
  4. Caprio S (2012). Calories from Soft Drinks – Do They Matter? The New England journal of medicine PMID: 22998341
  5. Changes to the protocol http://clinicaltrials.gov/archive/NCT00893529/2011_02_24/changes
  6. Overweight and Obesity: Childhood obesity facts  and A growing problem (www.cdc.gov)
  7. NRC Wim Köhler Eén kilo lichter.NRC | Zaterdag 22-09-2012 (http://archief.nrc.nl/)
  8.  The Best Study Design… For Dummies (http://laikaspoetnik.wordpress.com)
  9. Studies point to sugary drinks as culprits in childhood obesity – CTV News (ctvnews.ca)
  10. Hans van Maanen. Suiker uit fris, De Volkskrant, 29 september 2012 (freely accessible at http://www.vanmaanen.org/)
  11. Sugar-Sweetened Beverages, Diet Coke & Health. Part I. (http://laikaspoetnik.wordpress.com)
  12. Roni Caryn Rabina. Avoiding Sugared Drinks Limits Weight Gain in Two Studies. New York Times, September 21, 2012




RIP Statistician Paul Meier. Proponent not Father of the RCT.

14 08 2011

This headline in Boing Boing caught my eye today:  RIP Paul Meier, father of the randomized trial

Not surprisingly, I knew that Paul Meier (with Kaplan) introduced the Kaplan-Meier estimator (1958), a very important tool for measuring how many patients survive a medical treatment. But I didn’t know he was “father of the randomized trial”….

But is he really?:Father of the randomized trial and “probably best known for the introduction of randomized trials into the evaluation of medical treatments”, as Boing Boing states?

Boing Boing’s very short article is based on the New York Times article: Paul Meier, Statistician Who Revolutionized Medical Trials, Dies at 87. According to the NY Times “Dr. Meier was one of the first and most vocal proponents of what is called “randomization.” 

Randomization, the NY-Times explains, is:

Under the protocol, researchers randomly assign one group of patients to receive an experimental treatment and another to receive the standard treatment. In that way, the researchers try to avoid unintentionally skewing the results by choosing, for example, the healthier or younger patients to receive the new treatment.

(for a more detailed explanation see my previous posts The best study designs…. for dummies and #NotSoFunny #16 – Ridiculing RCTs & EBM)

Meier was a very successful proponent, that is for sure. According to Sir Richard Peto, (Dr. Meier) “perhaps more than any other U.S. statistician, was the one who influenced U.S. drug regulatory agencies, and hence clinical researchers throughout the U.S. and other countries, to insist on the central importance of randomized evidence.”

But an advocate need not be a father, for advocates are seldom the inventors/creators. A proponent is more of a nurse, a mentor or a … foster-parent.

Is Meier the true father/inventor of the RCT? And if not, who is?

Googling “Father of the randomized trial” won’t help, because all 1.610  hits point to Dr. Meier…. thanks to Boing Boing careless copying.

What I read so far doesn’t point at one single creator. And the RCT wasn’t just suddenly there. It started with comparison of treatments under controlled conditions. Back in 1753, the British naval surgeon James Lind published his famous account of 12 scurvy patients, “their cases as similar as I could get them” noting that “the most sudden and visible good effects were perceived from the uses of the oranges and lemons and that citrus fruit cured scurvy [3]. The French physician Pierre Louis and Harvard anatomist Oliver Wendell Holmes (19th century) were also fierce proponents of supporting conclusions about the effectiveness of treatments with statistics, not subjective impressions.[4]

But what was the first real RCT?

Perhaps the first real RCT was The Nuremberg salt test (1835) [6]. This was possibly not only the first RCT, but also the first scientific demonstration of the lack of effect of a homeopathic dilution. More than 50 visitors of a local tavern participated in the experiment. Half of them received a vial  filled with distilled snow water, the other half a vial with ordinary salt in a homeopathic C30-dilution of distilled snow water. None of the participants knew whether he got the “actual medicine or not” (blinding). The numbered vials were coded and the code was broken after the experiment (allocation concealment).

The first publications of RCT’s were in the field of psychology and agriculture. As a matter of fact one other famous statistician, Ronald A. Fisher  (of the Fisher’s exact test) seems to play a more important role in the genesis and popularization of RCT’s than Meier, albeit in agricultural research [5,7]. The book “The Lady Tasting Tea: How Statistics Revolutionized Science in the Twentieth Century” describes how Fisher devised a randomized trial at the spot to test the contention of a lady that she could taste the difference between tea into which milk had been poured and tea that had been poured into milk (almost according to homeopathic principles) [7]

According to Wikipedia [5] the published (medical) RCT appeared in the 1948 paper entitled “Streptomycin treatment of pulmonary tuberculosis”. One of the authors, Austin Bradford Hill, is (also) credited as having conceived the modern RCT.

Thus the road to the modern RCT is long, starting with the notions that experiments should be done under controlled conditions and that it doesn’t make sense to base treatment on intuition. Later, experiments were designed in which treatments were compared to placebo (or other treatments) in a randomized and blinded fashion, with concealment of allocation.

Paul Meier was not the inventor of the RCT, but a successful vocal proponent of the RCT. That in itself is commendable enough.

And although the Boing Boing article was incorrect, and many people googling for “father of the RCT” will find the wrong answer from now on, it did raise my interest in the history of the RCT and the role of statisticians in the development of science and clinical trials.
I plan to read a few of the articles and books mentioned below. Like the relatively lighthearted “The Lady Tasting Tea” [7]. You can envision a book review once I have finished reading it.

Note added 15-05 13.45 pm:

Today a more accurate article appeared in the Boston Globe (“Paul Meier; revolutionized medical studies using math”), which does justice to the important role of Dr Meier in the espousal of randomization as an essential element in clinical trials. For that is what he did.

Quote:

Dr. Meier published a scathing paper in the journal Science, “Safety Testing of Poliomyelitis Vaccine,’’ in which he described deficiencies in the production of vaccines by several companies. His paper was seen as a forthright indictment of federal authorities, pharmaceutical manufacturers, and the National Foundation for Infantile Paralysis, which funded the research for a polio vaccine.

  1. RIP Paul Meier, father of the randomized trial (boingboing.net)
  2. Paul Meier, Statistician Who Revolutionized Medical Trials, Dies at 87 (nytimes.com)
  3. M L Meldrum A brief history of the randomized controlled trial. From oranges and lemons to the gold standard. Hematology/ Oncology Clinics of North America (2000) Volume: 14, Issue: 4, Pages: 745-760, vii PubMed: 10949771  or see http://www.mendeley.com
  4. Fye WB. The power of clinical trials and guidelines,and the challenge of conflicts of interest. J Am Coll Cardiol. 2003 Apr 16;41(8):1237-42. PubMed PMID: 12706915. Full text
  5. http://en.wikipedia.org/wiki/Randomized_controlled_trial
  6. Stolberg M (2006). Inventing the randomized double-blind trial: The Nuremberg salt test of 1835. JLL Bulletin: Commentaries on the history of treatment evaluation (www.jameslindlibrary.org).
  7. The Lady Tasting Tea: How Statistics Revolutionized Science in the Twentieth Century Peter Cummings, MD, MPH, Jama 2001;286(10):1238-1239. doi:10.1001/jama.286.10.1238  Book Review.
    Book by David Salsburg, 340 pp, with illus, $23.95, ISBN 0-7167-41006-7, New York, NY, WH Freeman, 2001.
  8. Kaptchuk TJ. Intentional ignorance: a history of blind assessment and placebo controls in medicine. Bull Hist Med. 1998 Fall;72(3):389-433. PubMed PMID: 9780448. abstract
  9. The best study design for dummies/ (http://laikaspoetnik.wordpress.com: 2008/08/25/)
  10. #Notsofunny: Ridiculing RCT’s and EBM (http://laikaspoetnik.wordpress.com: 2010/02/01/)
  11. RIP Paul Meier : Research Randomization Advocate (mystrongmedicine.com)
  12. If randomized clinical trials don’t show that your woo works, try anthropology! (scienceblogs.com)
  13. The revenge of “microfascism”: PoMo strikes medicine again (scienceblogs.com)




How will we ever keep up with 75 Trials and 11 Systematic Reviews a Day?

6 10 2010

ResearchBlogging.orgAn interesting paper was published in PLOS Medicine [1]. As an information specialist and working part time for the Cochrane Collaboration* (see below), this topic is close to my heart.

The paper, published in PLOS Medicine is written by Hilda Bastian and two of my favorite EBM devotees ànd critics, Paul Glasziou and Iain Chalmers.

Their article gives an good overview of the rise in number of trials, systematic reviews (SR’s) of interventions and of medical papers in general. The paper (under the head: Policy Forum) raises some important issues, but the message is not as sharp and clear as usual.

Take the title for instance.

Seventy-Five Trials and Eleven Systematic Reviews a Day:
How Will We Ever Keep Up?

What do you consider its most important message?

  1. That doctors suffer from an information overload that is only going to get worse, as I did and probably also in part @kevinclauson who tweeted about it to medical librarians
  2. that the solution to this information overload consists of Cochrane systematic reviews (because they aggregate the evidence from individual trials) as @doctorblogs twittered
  3. that it is just about “too many systematic reviews (SR’s) ?”, the title of the PLOS-press release (so the other way around),
  4. That it is about too much of everything and the not always good quality SR’s: @kevinclauson and @pfanderson discussed that they both use the same ” #Cochrane Disaster” (see Kevin’s Blog) in their  teaching.
  5. that Archie Cochrane’s* dream is unachievable and ought perhaps be replaced by something less Utopian (comment by Richard Smith, former editor of the BMJ: 1, 3, 4, 5 together plus a new aspect: SR’s should not only  include randomized controlled trials (RCT’s)

The paper reads easily, but matters of importance are often only touched upon.  Even after reading it twice, I wondered: a lot is being said, but what is really their main point and what are their answers/suggestions?

But lets look at their arguments and pieces of evidence. (Black is from their paper, blue my remarks)

The landscape

I often start my presentations “searching for evidence” by showing the Figure to the right, which is from an older PLOS-article. It illustrates the information overload. Sometimes I also show another slide, with (5-10 year older data), saying that there are 55 trials a day, 1400 new records added per day to MEDLINE and 5000 biomedical articles a day. I also add that specialists have to read 17-22 articles a day to keep up to date with the literature. GP’s even have to read more, because they are generalists. So those 75 trials and the subsequent information overload is not really a shock to me.

Indeed the authors start with saying that “Keeping up with information in health care has never been easy.” The authors give an interesting overview of the driving forces for the increase in trials and the initiation of SR’s and critical appraisals to synthesize the evidence from all individual trials to overcome the information overload (SR’s and other forms of aggregate evidence decrease the number needed to read).

In box 1 they give an overview of the earliest systematic reviews. These SR’s often had a great impact on medical practice (see for instance an earlier discussion on the role of the Crash trial and of the first Cochrane review).
They also touch upon the institution of the Cochrane Collaboration.  The Cochrane collaboration is named after Archie Cochrane who “reproached the medical profession for not having managed to organise a “critical summary, by speciality or subspecialty, adapted periodically, of all relevant randomised controlled trials” He inspired the establishment of the international Oxford Database of Perinatal Trials and he encouraged the use of systematic reviews of randomized controlled trials (RCT’s).

A timeline with some of the key events are shown in Figure 1.

Where are we now?

The second paragraph shows many, interesting, graphs (figs 2-4).

Annoyingly, PLOS only allows one sentence-legends. The details are in the (WORD) supplement without proper referral to the actual figure numbers. Grrrr..!  This is completely unnecessary in reviews/editorials/policy forums. And -as said- annoying, because you have to read a Word file to understand where the data actually come from.

Bastian et al. have used MEDLINE’s publication types (i.e. case reports [pt], reviews[pt], Controlled Clinical Trial[pt] ) and search filters (the Montori SR filter and the Haynes narrow therapy filter, which is built-in in PubMed’s Clinical Queries) to estimate the yearly rise in number of study types. The total number of Clinical trials in CENTRAL (the largest database of controlled clinical trials, abbreviated as CCTRS in the article) and the Cochrane Database of Systematic Reviews (CDSR) are easy to retrieve, because the numbers are published quaterly (now monthly) by the Cochrane Library. Per definition, CDSR only contains SR’s and CENTRAL (as I prefer to call it) contains almost invariably controlled clinical trials.

In short, these are the conclusions from their three figures:

  • Fig 2: The number of published trials has raised sharply from 1950 till 2010
  • Fig 3: The number of systematic reviews and meta-analysis has raised tremendously as well
  • Fig 4: But systematic reviews and clinical trials are still far outnumbered by narrative reviews and case reports.

O.k. that’s clear & they raise a good point : an “astonishing growth has occurred in the number of reports of clinical trials since the middle of the 20th century, and in reports of systematic reviews since the 1980s—and a plateau in growth has not yet been reached.
Plus indirectly: the increase in systematic reviews  didn’t lead to a lower the number of trials and narrative reviews. Thus the information overload is still increasing.
But instead of discussing these findings they go into an endless discussion on the actual data and the fact that we “still do not know exactly how many trials have been done”, to end the discussion by saying that “Even though these figures must be seen as more illustrative than precise…” And than you think. So what? Furthermore, I don’t really get their point of this part of their article.

 

Fig. 2: The number of published trials, 1950 to 2007.

 

 

With regard to Figure 2 they say for instance:

The differences between the numbers of trial records in MEDLINE and CCTR (CENTRAL) (see Figure 2) have multiple causes. Both CCTR and MEDLINE often contain more than one record from a single study, and there are lags in adding new records to both databases. The NLM filters are probably not as efficient at excluding non-trials as are the methods used to compile CCTR. Furthermore, MEDLINE has more language restrictions than CCTR. In brief, there is still no single repository reliably showing the true number of randomised trials. Similar difficulties apply to trying to estimate the number of systematic reviews and health technology assessments (HTAs).

Sorry, although some of these points may be true, Bastian et al. don’t go into the main reason for the difference between both graphs, that is the higher number of trial records in CCTR (CENTRAL) than in MEDLINE: the difference can be simply explained by the fact that CENTRAL contains records from MEDLINE as well as from many other electronic databases and from hand-searched materials (see this post).
With respect to other details:. I don’t know which NLM filter they refer to, but if they mean the narrow therapy filter: this filter is specifically meant to find randomized controlled trials, and is far more specific and less sensitive than the Cochrane methodological filters for retrieving controlled clinical trials. In addition, MEDLINE does not have more language restrictions per se: it just contains a (extensive) selection of  journals. (Plus people more easily use language limits in MEDLINE, but that is besides the point).

Elsewhere the authors say:

In Figures 2 and 3 we use a variety of data sources to estimate the numbers of trials and systematic reviews published from 1950 to the end of 2007 (see Text S1). The number of trials continues to rise: although the data from CCTR suggest some fluctuation in trial numbers in recent years, this may be misleading because the Cochrane Collaboration virtually halted additions to CCTR as it undertook a review and internal restructuring that lasted a couple of years.

As I recall it , the situation is like this: till 2005 the Cochrane Collaboration did the so called “retag project” , in which they searched for controlled clinical trials in MEDLINE and EMBASE (with a very broad methodological filter). All controlled trials articles were loaded in CENTRAL, and the NLM retagged the controlled clinical trials that weren’t tagged with the appropriate publication type in MEDLINE. The Cochrane stopped the laborious retag project in 2005, but still continues the (now) monthly electronic search updates performed by the various Cochrane groups (for their topics only). They still continue handsearching. So they didn’t (virtually?!) halted additions to CENTRAL, although it seems likely that stopping the retagging project caused the plateau. Again the author’s main points are dwarfed by not very accurate details.

Some interesting points in this paragraph:

  • We still do not know exactly how many trials have been done.
  • For a variety of reasons, a large proportion of trials have remained unpublished (negative publication bias!) (note: Cochrane Reviews try to lower this kind of bias by applying no language limits and including unpublished data, i.e. conference proceedings, too)
  • Many trials have been published in journals without being electronically indexed as trials, which makes them difficult to find. (note: this has been tremendously improved since the Consort-statement, which is an evidence-based, minimum set of recommendations for reporting RCTs, and by the Cochrane retag-project, discussed above)
  • Astonishing growth has occurred in the number of reports of clinical trials since the middle of the 20th century, and in reports of systematic reviews since the 1980s—and a plateau in growth has not yet been reached.
  • Trials are now registered in prospective trial registers at inception, theoretically enabling an overview of all published and unpublished trials (note: this will also facilitate to find out reasons for not publishing data, or alteration of primary outcomes)
  • Once the International Committee of Medical Journal Editors announced that their journals would no longer publish trials that had not been prospectively registered, far more ongoing trials were being registered per week (200 instead of 30). In 2007, the US Congress made detailed prospective trial registration legally mandatory.

The authors do not discuss that better reporting of trials and the retag project might have facilitated the indexing and retrieval of trials.

How Close Are We to Archie Cochrane’s Goal?

According to the authors there are various reasons why Archie Cochrane’s goal will not be achieved without some serious changes in course:

  • The increase in systematic reviews didn’t displace other less reliable forms of information (Figs 3 and 4)
  • Only a minority of trials have been assessed in systematic review
  • The workload involved in producing reviews is increasing
  • The bulk of systematic reviews are now many years out of date.

Where to Now?

In this paragraph the authors discuss what should be changed:

  • Prioritize trials
  • Wider adoption of the concept that trials will not be supported unless a SR has shown the trial to be necessary.
  • Prioritizing SR’s: reviews should address questions that are relevant to patients, clinicians and policymakers.
  • Chose between elaborate reviews that answer a part of the relevant questions or “leaner” reviews of most of what we want to know. Apparently the authors have already chosen for the latter: they prefer:
    • shorter and less elaborate reviews
    • faster production ànd update of SR’s
    • no unnecessary inclusion of other study types other than randomized trials. (unless it is about less common adverse effects)
  • More international collaboration and thereby a better use  of resources for SR’s and HTAs. As an example of a good initiative they mention “KEEP Up,” which will aim to harmonise updating standards and aggregate updating results, initiated and coordinated by the German Institute for Quality and Efficiency in Health Care (IQWiG) and involving key systematic reviewing and guidelines organisations such as the Cochrane Collaboration, Duodecim, the Scottish Intercollegiate Guidelines Network (SIGN), and the National Institute for Health and Clinical Excellence (NICE).

Summary and comments

The main aim of this paper is to discuss  to which extent the medical profession has managed to make “critical summaries, by speciality or subspeciality, adapted periodically, of all relevant randomized controlled trials”, as proposed 30 years ago by Archie Cochrane.

Emphasis of the paper is mostly on the number of trials and systematic reviews, not on qualitative aspects. Furthermore there is too much emphasis on the methods determining the number of trials and reviews.

The main conclusion of the authors is that an astonishing growth has occurred in the number of reports of clinical trials as well as in the number of SR’s, but that these systematic pieces of evidence shrink into insignificance compared to the a-systematic narrative reviews or case reports published. That is an important, but not an unexpected conclusion.

Bastian et al don’t address whether systematic reviews have made the growing number of trials easier to access or digest. Neither do they go into developments that have facilitated the retrieval of clinical trials and aggregate evidence from databases like PubMed: the Cochrane retag-project, the Consort-statement, the existence of publication types and search filters (they use themselves to filter out trials and systematic reviews). They also skip other sources than systematic reviews, that make it easier to find the evidence: Databases with Evidence Based Guidelines, the TRIP database, Clinical Evidence.
As Clay Shirky said: “It’s Not Information Overload. It’s Filter Failure.”

It is also good to note that case reports and narrative reviews serve other aims. For medical practitioners rare case reports can be very useful for their clinical practice and good narrative reviews can be valuable for getting an overview in the field or for keeping up-to-date. You just have to know when to look for what.

Bastian et al have several suggestions for improvement, but these suggestions are not always underpinned. For instance, they propose access to all systematic reviews and trials. Perfect. But how can this be attained? We could stimulate authors to publish their trials in open access papers. For Cochrane reviews this would be desirable but difficult, as we cannot demand from authors who work for months for free to write a SR to pay the publications themselves. The Cochrane Collab is an international organization that does not receive subsidies for this. So how could this be achieved?

In my opinion, we can expect the most important benefits from prioritizing of trials ànd SR’s, faster production ànd update of SR’s, more international collaboration and less duplication. It is a pity the authors do not mention other projects than “Keep up”.  As discussed in previous posts, the Cochrane Collaboration also recognizes the many issues raised in this paper, and aims to speed up the updates and to produce evidence on priority topics (see here and here). Evidence aid is an example of a successful effort.  But this is only the Cochrane Collaboration. There are many more non-Cochrane systematic reviews produced.

And then we arrive at the next issue: Not all systematic reviews are created equal. There are a lot of so called “systematic reviews”, that aren’t the conscientious, explicit and judicious created synthesis of evidence as they ought to be.

Therefore, I do not think that the proposal that each single trial should be preceded by a systematic review, is a very good idea.
In the Netherlands writing a SR is already required for NWO grants. In practice, people just approach me, as a searcher, the days before Christmas, with the idea to submit the grant proposal (including the SR) early in January. This evidently is a fast procedure, but doesn’t result in a high standard SR, upon which others can rely.

Another point is that this simple and fast production of SR’s will only lead to a larger increase in number of SR’s, an effect that the authors wanted to prevent.

Of course it is necessary to get a (reliable) picture of what has already be done and to prevent unnecessary duplication of trials and systematic reviews. It would the best solution if we would have a triplet (nano-publications)-like repository of trials and systematic reviews done.

Ideally, researchers and doctors should first check such a database for existing systematic reviews. Only if no recent SR is present they could continue writing a SR themselves. Perhaps it sometimes suffices to search for trials and write a short synthesis.

There is another point I do not agree with. I do not think that SR’s of interventions should only include RCT’s . We should include those study types that are relevant. If RCT’s furnish a clear proof, than RCT’s are all we need. But sometimes – or in some topics/specialties- RCT’s are not available. Inclusion of other study designs and rating them with GRADE (proposed by Guyatt) gives a better overall picture. (also see the post: #notsofunny: ridiculing RCT’s and EBM.

The authors strive for simplicity. However, the real world isn’t that simple. In this paper they have limited themselves to evidence of the effects of health care interventions. Finding and assessing prognostic, etiological and diagnostic studies is methodologically even more difficult. Still many clinicians have these kinds of questions. Therefore systematic reviews of other study designs (diagnostic accuracy or observational studies) are also of great importance.

In conclusion, whereas I do not agree with all points raised, this paper touches upon a lot of important issues and achieves what can be expected from a discussion paper:  a thorough shake-up and a lot of discussion.

References

  1. Bastian, H., Glasziou, P., & Chalmers, I. (2010). Seventy-Five Trials and Eleven Systematic Reviews a Day: How Will We Ever Keep Up? PLoS Medicine, 7 (9) DOI: 10.1371/journal.pmed.1000326

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The Placebo & Homeopathy effects

9 03 2010

Ben Goldacre is the man behind the book “Bad Science“, the blog “Bad Science” (http://www.badscience.net/) and the weekly Bad Science column in the Guardian. He is a medical doctor who specializes in unpicking dodgy scientific claims made by scaremongering journalists, dodgy government reports, evil pharmaceutical corporations, PR companies and quacks.

One of Ben’s favorite subjects is “the placebo effect”.  He wrote a two-part documentary series called The Placebo Effect on BBC Radio 4.

Recently Ben also made a short video, released by NHSChoices, on the placebo effect. Here he explains this difficult topic in a clear and comprehensible fashion.

Somehow I always think of Ben as his logo suggests: dr. Frankenstein. It is a relief to see that dr. Ben is almost the opposite: friendly, enthusiastic and crystal clear (without needing a crystal ball ;).

The video is not only recommended for people who don’t have a clue about the placebo effect but also for those (like me) who already know that a placebo is a dummy treatment.
Did you know, for instance, that one placebo can be more effective than another, depending on your expectations or the color of the capsule/pill or the expectations of the one who treats you?

Seeing the video I wondered in what respect homeopathy would differ from the placebo.

And you know what? Ben Goldacre explains that too in an older video. Really wonderful how “magically” homeopathic dilutions are graphically explained.

———

The first video has been tweeted about and blogged about several times. First that was a reason not to blog about it. But on the other hand the topic is well suited for this blog and many people who aren’t on Twitter or don’t follow those blogs might like it anyway.

To you my dear reader the following question: do you like me to include such videos, short notes or  trendy topics on my blog alternating with the longer in depth posts)?





#NotSoFunny #16 – Ridiculing RCTs & EBM

1 02 2010

I remember it well. As a young researcher I presented my findings in one of my first talks, at the end of which the chair killed my work with a remark, that made the whole room of scientists laugh, but was really beside the point. My supervisor, a truly original and very wise scientist, suppressed his anger. Afterwards, he said: “it is very easy ridiculing something that isn’t a mainstream thought. It’s the argument that counts. We will prove that we are right.” …And we did.

This was not my only encounter with scientists who try to win the debate by making fun of a theory, a finding or …people. But it is not only the witty scientist who is to *blame*, it is also the uncritical audience that just swallows it.

I have similar feelings with some journal articles or blog posts that try to ridicule EBM – or any other theory or approach. Funny, perhaps, but often misunderstood and misused by “the audience”.

Take for instance the well known spoof article in the BMJ:

“Parachute use to prevent death and major trauma related to gravitational challenge: systematic review of randomised controlled trials”

It is one of those Christmas spoof articles in the BMJ, meant to inject some medical humor into the normally serious scientific literature. The spoof parachute article pretends to be a Systematic Review of RCT’s  investigating if parachutes can prevent death and major trauma. Of course, no such trial has been done or will be done: dropping people at random with and without a parachute to proof that you better jump out of a plane with a parachute.

I found the article only mildly amusing. It is so unrealistic, that it becomes absurd. Not that I don’t enjoy absurdities at times, but  absurdities should not assume a live of their own.  In this way it doesn’t evoke a true discussion, but only worsens the prejudice some people already have.

People keep referring to this 2003 article. Last Friday, Dr. Val (with whom I mostly agree) devoted a Friday Funny post to it at Get Better Health: “The Friday Funny: Why Evidence-Based Medicine Is Not The Whole Story”.* In 2008 the paper was also discussed by Not Totally Rad [3]. That EBM is not the whole story seems pretty obvious to me. It was never meant to be…

But lets get specific. Which assumptions about RCT’s and SR’s are wrong, twisted or put out of context? Please read the excellent comments below the article. These often put the finger on the spot.

1. EBM is cookbook medicine.
Many define EBM as “make clinical decisions based on a synthesis of the best available evidence about a treatment.” (i.e. [3]). However, EBM is not cookbook medicine.

The accepted definition of EBM  is “the conscientious, explicit and judicious use of current best evidence in making decisions about the care of individual patients” [4]. Sacket already emphasized back in 1996:

Good doctors use both individual clinical expertise and the best available external evidence, and neither alone is enough. Without clinical expertise, practice risks becoming tyrannised by evidence, for even excellent external evidence may be inapplicable to or inappropriate for an individual patient. Without current best evidence, practice risks becoming rapidly out of date, to the detriment of patients.


2. RCT’s are required for evidence.

Although a well performed RCT provides the “best” evidence, RCT’s are often not appropriate or indicated. That is especially true for domains other than therapy. In case of prognostic questions the most appropriate study design is usually an inception cohort. A RCT for instance can’t tell whether female age is a prognostic factor for clinical pregnancy rates following IVF: there is no way to randomize for “age”, or for “BMI”. ;)

The same is true for etiologic or harm questions. In theory, the “best” answer is obtained by RCT. However RCT’s are often unethical or unnecessary. RCT’s are out of the question to address whether substance X causes cancer. Observational studies will do. Sometimes cases provide sufficient evidence. If a woman gets hepatic veno-occlusive disease after drinking loads of a herbal tea the finding of  similar cases in the literature may be sufficient to conclude that the herbal tea probably caused the disease.

Diagnostic accuracy studies also require another study design (cross-sectional study, or cohort).

But even in the case of  interventions, we can settle for less than a RCT. Evidence is not present or not, but exists on a hierarchy. RCT’s (if well performed) are the most robust, but if not available we have to rely on “lower” evidence.

BMJ Clinical Evidence even made a list of clinical questions unlikely to be answered by RCT’s. In this case Clinical Evidence searches and includes the best appropriate form of evidence.

  1. where there are good reasons to think the intervention is not likely to be beneficial or is likely to be harmful;
  2. where the outcome is very rare (e.g. a 1/10000 fatal adverse reaction);
  3. where the condition is very rare;
  4. where very long follow up is required (e.g. does drinking milk in adolescence prevent fractures in old age?);
  5. where the evidence of benefit from observational studies is overwhelming (e.g. oxygen for acute asthma attacks);
  6. when applying the evidence to real clinical situations (external validity);
  7. where current practice is very resistant to change and/or patients would not be willing to take the control or active treatment;
  8. where the unit of randomisation would have to be too large (e.g. a nationwide public health campaign); and
  9. where the condition is acute and requires immediate treatment.
    Of these, only the first case is categorical. For the rest the cut off point when an RCT is not appropriate is not precisely defined.

Informed health decisions should be based on good science rather than EBM (alone).

Dr Val [2]: “EBM has been an over-reliance on “methodolatry” – resulting in conclusions made without consideration of prior probability, laws of physics, or plain common sense. (….) Which is why Steve Novella and the Science Based Medicine team have proposed that our quest for reliable information (upon which to make informed health decisions) should be based on good science rather than EBM alone.

Methodolatry is the profane worship of the randomized clinical trial as the only valid method of investigation. This is disproved in the previous sections.

The name “Science Based Medicine” suggests that it is opposed to “Evidence Based Medicine”. At their blog David Gorski explains: “We at SBM believe that medicine based on science is the best medicine and tirelessly promote science-based medicine through discussion of the role of science and medicine.”

While this may apply to a certain extent to quack or homeopathy (the focus of SBM) there are many examples of the opposite: that science or common sense led to interventions that were ineffective or even damaging, including:

As a matter of fact many side-effects are not foreseen and few in vitro or animal experiments have led to successful new treatments.

At the end it is most relevant to the patient that “it works” (and the benefits outweigh the harms).

Furthermore EBM is not -or should not be- without consideration of prior probability, laws of physics, or plain common sense. To me SBM and EBM are not mutually exclusive.

Why the example is bullshit unfair and unrealistic

I’ll leave it to the following comments (and yes the choice is biased) [1]

Nibu A George,Scientist :

First of all generalizing such reports of some selected cases and making it a universal truth is unhealthy and challenging the entire scientific community. Secondly, the comparing the parachute scenario with a pure medical situation is unacceptable since the parachute jump is rather a physical situation and it become a medical situation only if the jump caused any physical harm to the person involved.

Richard A. Davidson, MD,MPH:

This weak attempt at humor unfortunately reinforces one of the major negative stereotypes about EBM….that RCT’s are required for evidence, and that observational studies are worthless. If only 10% of the therapies that are paraded in front of us by journals were as effective as parachutes, we would have much less need for EBM. The efficacy of most of our current therapies are only mildly successful. In fact, many therapies can provide only a 25% or less therapeutic improvement. If parachutes were that effective, nobody would use them.
While it’s easy enough to just chalk this one up to the cliche of the cantankerous British clinician, it shows a tremendous lack of insight about what EBM is and does. Even worse, it’s just not funny.

Aviel Roy-Shapira, Senior Staff Surgeon

Smith and Pell succeeded in amusing me, but I think their spoof reflects a common misconception about evidence based medicine. All too many practitioners equate EBM with randomized controlled trials, and metaanalyses.
EBM is about what is accepted as evidence, not about how the evidence is obtained. For example, an RCT which shows that a given drug lowers blood pressure in patients with mild hypertension, however well designed and executed, is not acceptable as a basis for treatment decisions. One has to show that the drug actually lowers the incidence of strokes and heart attacks.
RCT’s are needed only when the outcome is not obvious. If most people who fall from airplanes without a parachute die, this is good enough. There is plenty of evidence for that.

EBM is about using outcome data for making therapeutic decisions. That data can come from RCTs but also from observation

Lee A. Green, Associate Professor

EBM is not RCTs. That’s probably worth repeating several times, because so often both EBM’s detractors and some of its advocates just don’t get it. Evidence is not binary, present or not, but exists on a heirarchy (Guyatt & Rennie, 2001). (….)
The methods and rigor of EBM are nothing more or less than ways of correcting for our
imperfect perceptions of our experiences. We prefer, cognitively, to perceive causal connections. We even perceive such connections where they do not exist, and we do so reliably and reproducibly under well-known sets of circumstances. RCTs aren’t holy writ, they’re simply a tool for filtering out our natural human biases in judgment and causal attribution. Whether it’s necessary to use that tool depends upon the likelihood of such bias occurring.

Scott D Ramsey, Associate Professor

Parachutes may be a no-brainer, but this article is brainless.

Unfortunately, there are few if any parallels to parachutes in health care. The danger with this type of article is that it can lead to labeling certain medical technologies as “parachutes” when in fact they are not. I’ve already seen this exact analogy used for a recent medical technology (lung volume reduction surgery for severe emphysema). In uncontrolled studies, it quite literally looked like everyone who didn’t die got better. When a high quality randomized controlled trial was done, the treatment turned out to have significant morbidity and mortality and a much more modest benefit than was originally hypothesized.

Timothy R. Church, Professor

On one level, this is a funny article. I chuckled when I first read it. On reflection, however, I thought “Well, maybe not,” because a lot of people have died based on physicians’ arrogance about their ability to judge the efficacy of a treatment based on theory and uncontrolled observation.

Several high profile medical procedures that were “obviously” effective have been shown by randomized trials to be (oops) killing people when compared to placebo. For starters to a long list of such failed therapies, look at antiarrhythmics for post-MI arrhythmias, prophylaxis for T. gondii in HIV infection, and endarterectomy for carotid stenosis; all were proven to be harmful rather than helpful in randomized trials, and in the face of widespread opposition to even testing them against no treatment. In theory they “had to work.” But didn’t.

But what the heck, let’s play along. Suppose we had never seen a parachute before. Someone proposes one and we agree it’s a good idea, but how to test it out? Human trials sound good. But what’s the question? It is not, as the author would have you believe, whether to jump out of the plane without a parachute or with one, but rather stay in the plane or jump with a parachute. No one was voluntarily jumping out of planes prior to the invention of the parachute, so it wasn’t to prevent a health threat, but rather to facilitate a rapid exit from a nonviable plane.

Another weakness in this straw-man argument is that the physics of the parachute are clear and experimentally verifiable without involving humans, but I don’t think the authors would ever suggest that human physiology and pathology in the face of medication, radiation, or surgical intervention is ever quite as clear and predictable, or that non-human experience (whether observational or experimental) would ever suffice.

The author offers as an alternative to evidence-based methods the “common sense” method, which is really the “trust me, I’m a doctor” method. That’s not worked out so well in many high profile cases (see above, plus note the recent finding that expensive, profitable angioplasty and coronary artery by-pass grafts are no better than simple medical treatment of arteriosclerosis). And these are just the ones for which careful scientists have been able to do randomized trials. Most of our accepted therapies never have been subjected to such scrutiny, but it is breathtaking how frequently such scrutiny reveals problems.

Thanks, but I’ll stick with scientifically proven remedies.

parachute experiments without humans

* on the same day as I posted Friday Foolery #15: The Man who pioneered the RCT. What a coincidence.

** Don’t forget to read the comments to the article. They are often excellent.

Photo Credits

ReferencesResearchBlogging.org

  1. Smith, G. (2003). Parachute use to prevent death and major trauma related to gravitational challenge: systematic review of randomised controlled trials BMJ, 327 (7429), 1459-1461 DOI: 10.1136/bmj.327.7429.1459
  2. The Friday Funny: Why Evidence-Based Medicine Is Not The Whole Story”. (getbetterhealth.com) [2010.01.29]
  3. Call for randomized clinical trials of Parachutes (nottotallyrad.blogspot.com) [08-2008]
  4. Sackett DL, Rosenberg WM, Gray JA, Haynes RB, & Richardson WS (1996). Evidence based medicine: what it is and what it isn’t. BMJ (Clinical research ed.), 312 (7023), 71-2 PMID: 8555924
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are very well edged off




Friday Foolery #15: The Man who pioneered the RCT

29 01 2010

This BMJ video certainly belongs on a blog like this, focussing on EBM. This video shows “John Crofton who pioneered the randomised controlled trial in a 1948 BMJ paper which looked at the antibiotic streptomycin to treat TB. Now in his 90s, Dr Crofton talks to Colin Blakemore about the importance of randomisation and blinding, and how it has helped to make medicine more evidence based.”

First seen on the Clinical Cases and Images: CasesBlog of Ves Dimov.

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NOT ONE RCT on Swine Flu or H1N1?! – Outrageous!

16 12 2009

Last week doctorblogs (Annabel Bentley) tweeted: “Outrageous- there isn’t ONE randomised trial on swine flu or #H1N1

Annabel referred to an article at Trust the Evidence, the excellent blog of the Centre for Evidence-Based Medicine (CEBM) in Oxford, UK.

In the article “Is swine flu the most over-published and over-hyped disease ever?Carl Heneghan first showed the results of a quick PubMed search using the terms ‘swine flu’ and ‘H1N1’: this yielded 4,475 articles on the subject, with approximately one third (1,437 articles) published in the last 7 months (search: November 27th). Of these 107, largely news articles, were published in the BMJ, followed by the Lancet and NEJM at 35 each.

Top News stories on H1N1 generated appr. 2000 to 4000 news articles each (in Google). Items included outbreak of a new form of ‘swine flu’ which prompted the United States and the World Health Organization to declare a public health emergency (April), Southern Hemisphere being mostly spared in the swine flu epidemic (May), Tamiflu, i.e. the effects of Tamiflu in children in the BMJ (co-authored by Carl) in August and the availability of the vaccine H1N1 vaccine clinics to offer seasonal flu shots in November.

According to Heneghan this must be the most over-hyped disease ever, and he wonders: “are there any other infections out there?”

Finally he ends with: Do you know what the killer fact is in all of this? There isn’t one randomized trial out there on swine flu or H1N1 – outrageous.”

My first thoughts were: “is H1N1 really so over-published compared to other (infectious) diseases?”, “Is it really surprising that there are no RCTs yet? The H1N1-pandemics just started a few months ago!” and even “are RCT’s really the study designs we urgently need right now?”

Now the severity of the H1N1 flu seems less than feared, it is easy to be wise. Isn’t is logic that there are a lot of “exploratory studies” first: characterization of the virus, establishing the spread of H1N1 around the world, establishing mortality and morbidity, and patterns of vulnerability among the population? It is also understandable that a lot of news articles are published, in the BMJ or in online newspapers. We want to be informed. In the Netherlands we now have a small outbreak of Q-fever, partly because the official approach was slow and underestimated the public health implications of Q-fever. So the public was really underinformed. That is worse than being “overexposed”.

News often spreads like wildfire, that is no news. When I google “US Preventive Services Task Force” (who issued the controversial US breast cancer screening guidelines last month) 2,364 hits still pop up in Google News (over the last month). All papers and other news sources echo the news. 2,000 hits are easily reached.

4,475 PubMed articles on ‘swine flu’ and ‘H1N1’ isn’t really that much. When I quickly search PubMed for the rather “new” disease Q-fever I get 3,752 hits, a search for HPV (Alphapapillomavirus OR papilloma infections OR HPV OR human papilloma virus) gives 19,543 hits (1,330 over the last 9 months), and a quick search for (aids) AND “last 9 months”[edat] yields 4,073 hits!

The number of hits alone doesn’t mean much, certainly not if news, editorials and comments are included. But lets go to the second comment, that there is “not ONE RCT on H1N1.”

Again, is it reasonable to expect ONE RCT published and included in PubMed over a 9 month period? Any serious study takes time from concept to initiation, patient-enrollment, sufficient follow-up, collection of data, writing and submitting the article, peer review, publication, inclusion in PubMed and assignment of MeSH-terms (including the publication type “Randomized Controlled Trial”).

Furthermore RCTs are not always the most feasible or appropriate study designs for answering certain questions. For instance for questions related to harm, etiology, epidemiology, spreading of virus, characteristics, diagnosis and prognosis. RCTs may be most suitable to evaluate the efficacy of treatment or prevention interventions. Thus in case of H1N1 the efficacy of vaccines and of neuraminidase inhibitors to prevent or treat H1N1 flu. However, it may not always be ethical to do so (see below).

I’ve repeated the search, and using prefab “My NCBI filters” for RCTs discussed before I get the following results:

Using the Randomized Controlled Trials limits in PubMed I do get 7 hits, and using broader filters, like the Therapy/Narrow Filter under  Clinical Queries I even find 2 more RCTs that have not yet been indexed by PubMed. With the Cochrane Highly sensitive Filter even more hits are obtained, most of which are “noise”, inherent to the use of a broad filter.

The found RCTs are safety/immunogenicity/stability studies of subunit or split vaccines to H1N1, H3N2, and B influenza strains. This means they are not restricted to H1N1, but this is true for the entire set of H1N1 publications. 40 of the 1443 hits are even animal studies. Thus the total number of articles dealing with H1N1 only -and in humans- is far less than 1443.
By the way, one of the 15 H1N1-hits in PubMed obtained with the SR-filter (see Fig) is a meta-analysis of RCTs in the BMJ, co-authored by Heneghan. It is not about H1N1, but contains the sentence: “Their (neuraminidase inhibitors) effects on the incidence of serious complications, and on the current A/H1N1 influenza strain remain to be determined.”

More important, if studies have been undertaken in this field they are probably not yet published. Thus, the place to look is a clinical trials register, like Clinical trials.gov (http://clinicaltrials.gov/), The International Clinical Registry Platform Search Portal at the WHO (www.who.int/trialsearch) , national or pharmaceutical industry trials registers.

A search for H1N1 OR swine flu in Clinical trials.gov, that offers the best searching functions, yields 132 studies, of which 116 were first recieved this year.

Again, most trials concern the safety and efficacy of H1N1 vaccines and include the testing of vaccines on subgroups, like pregnant women, children with asthma and people with AIDS. 30 trials are phase III.
Narrowing the search to H1N1
OR swine flu | neuraminidase inhibitors OR oseltamivir OR zanamivir (treatment filled in in the filed “Interventions”) yields 8 studies. One of the studies is a phase III trial.

This yield doesn’t seem bad per se. However, numbers of trials don’t mean a lot and a more pertinent issue is, whether the most important and urgent questions are investigated.

Three issues are important with respect to interventions:

  1. Are H1N1 vaccines safe and immunogenic? in subpopulations?
  2. Do H1N1 vaccines lower morbidity and mortality due to the H1N1 flu?
  3. Are neuraminidase inhibitors effective in preventing or treating H1N1 flu?
Question [1] will be answered by current trials.
Older Cochrane Reviews on the seasonal influenza flu (and updates) cast doubt on the efficacy of [2] vaccines (see the [poor*] Atlantic news article) ànd [2] neuraminidase inhibitors in children (Cochrane 2007 and BMJ 2009) ànd adults  (Cochrane 2006, update 2008 and BMJ 2009) against symptoms or complications of the seasonal flu. The possibility has even been raised that seasonal flu shots are linked to swine flu risk.
However, the current H1N1 isn’t a seasonal flu. It is a sudden, new pandemic that requires different actions. Overall H1N1 isn’t as deadly as the regular influenza strains, but it hits certain people harder: very young kids, people with asthma and pregnant women. About the latter group, Amy Tuteur (obstetrician-gynecologist blogging at The Skeptical OB) wrote a guest post at Kevin MD:
(…) the H1N1 influenza has had an unexpectedly devastating impact among pregnant women. According to the CDC, there have been approximately 700 reported cases of H1N1 in pregnant women since April.** Of these, 100 women have required admission to an intensive care unit and 28 have died. In other words, 1 out of every 25 pregnant women who contracted H1N1 died of it. By any standard, that is an appalling death rate. (……)
To put it in perspective, the chance of a pregnant woman dying from H1N1 is greater than the chance of a heart patient dying during triple bypass surgery. That is not a trivial risk.
The H1N1 flu has taken an extraordinary toll among pregnant women. A new vaccine is now available. Because of the nature of the emergency, there has not been time to do any long term studies of the vaccine. Yet pregnant women will need to make a decision as soon as possible on whether to be vaccinated. (Emphasis mine)
…. Given the dramatic threat and the fact that we know of no unusual complications of vaccination, the decision seems clear. Every pregnant woman should get vaccinated as soon as possible.
Thus the anticipated risks must be balanced against the anticipated benefits, Amy urges pregnant women to get vaccinated, even though no one can be sure about side effects ànd about the true efficacy of the vaccine.
For scientific purposes it would be best to perform a double randomized trial with half of a series of pregnant women receiving the vaccine, and the other half a placebo. This would provide the most rigid evidence for the true efficacy and safety of the vaccine.
However it would not be ethical to do so. As “Orac” of Orac Knows explains so well  in his post “Vaccination for H1N1 “swine” flu: Do The Atlantic, Shannon Brownlee, and Jeanne Lenzer matter?” RCTs are only acceptable from an ethical standpoint if we truly do not know whether one treatment is superior to another or a treatment is better than a placebo. There is sufficient reason to believe that vaccination for H1N1 will be more efficacious than “doing nothing”. Leaving a control group unvaccinated will certainly mean that a substantial percentage of pregnant women is going to die. To study the efficacy of the H1N1 among pregnant women observational studies (like cohort studies) are also suitable and more appropriate.
Among the studies found in ClinicalTrials.gov there are a few H1N1 Vaccine Clinical Studies in Pregnant Women, including RCTs. But these RCT’s never compare vaccinated women with a non-vaccinated women. All pregnant women are vaccinated, but the conditions vary.
In one Danish study the arms (study groups) are as follows:
Thus two doses of H1N1 with adjuvant are compared with a higher dose H1N1 without adjuvant. As a control non-pregnant women are vaccinated with the adjuvant H1N1.*** The RCT is performed within a prospective, birth-cohort study recruiting 800 pregnant mothers between Q1- 2009 and Q4-2010. As a natural control women pregnant in the H1N1 season (Q4) will be compared with women outside the season. Please note that the completion date of this study will be 2012, thus we will have to wait a number of years before the study describing the results will be found in PubMed….
To give an impression of the idea behind the study, here is the summary of that trial in the register (not because it is particularly outstanding, but to highlight the underlying thoughts):
“Pregnant women are at particular risk during the imminent H1N1v influenza pandemic. The new H1N1v virus requires urgent political and medical decisions on vaccination strategies in order to minimize severe disease and death from this pandemic. However, there is a lack of evidence to build such decisions upon. A vaccine will be provided in the fourth quarter of 2009, but there is little knowledge on the immunogenicity. Particularly its clinical effectiveness and duration of immunity in pregnant women and their newborn infants is unknown. Therefore, it will be important to study the optimal vaccination regimens with respect to dosing and use of adjuvant to decide future health policies on vaccination of pregnant women. We have a unique possibility to study these aspects of H1N1v infection in pregnant women in our ongoing unselected, prospective, birth-cohort study recruiting 800 pregnant mothers between Q1- 2009 and Q4-2010. Pregnant women from East-Denmark are being enrolled during the 2nd trimester and their infant will undergo a close clinical follow-up. The H1N1v pandemic is expected to reach Denmark Q4-2009. The timing of this enrollment and the imminent pandemic allows for an “experiment of nature” whereby the first half of the mothers completes pregnancy before the H1N1v pandemic. The other half of this cohort will be pregnant while H1N1v is prevalent in the community and will require H1N1v vaccination.The aim of this randomized, controlled, trial is to compare and evaluate the dose-related immune protection conferred by vaccine and adjuvant (Novartis vaccine Focetria) in pregnant women and non-pregnant women. In addition the protocol will assess the passive immunity conferred to the newborn from these vaccine regimes. The study will provide evidence-based guidance for health policies on vaccination for the population of pregnant women during future H1N1v pandemics.”
Although with regard to H1N1-vaccination, appropriate studies are being done, it is feasible that certain measures might not be appropriate on basis of what we know. For instance, pretreating people in the non-risk groups (healthy young adults) with neuraminidase-inhibitors, because they are “indispensable employees”. Perhaps Heneghan, who as you remember is a co-author of the BMJ paper on neuraminidase -inhibitors in children with the seasonal flu, was thinking of this when writing his post.
If Heneghan would have directed his arrows at certain interventions in certain circumstances in certain people he might have had a good point, but now his arrows don’t hit any target. Revere from Effect Measure and Orac from Orac Knows might well have diagnosed him as someone who suffers from “methodolatry,” which is, as Revere puts it, the “profane worship of the randomized clinical trial as the only valid method of investigation.”
Notes
* But see the excellent post of Orac who trashes the Atlantic paper in Flu vaccination: Do The Atlantic, Shannon Brownlee, and Jeanne Lenzer matter? (scienceblogs.com). He also critiques the attitude of the Cochrane author Jefferson, who has a different voice in the media compared to the Cochrane Reviews he co-authors. Here he is far more neutral.
** There is no direct link to the data in the post. I’m not sure whether all pregnant women in the US are routinely tested for H1N1. (if not the percentage of H1N1 deaths among H1N1 infected pregnant women might be overestimated)
***In the US, vaccins given to pregnant women are without adjuvant.

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Does the insulin Lantus (glargine) cause cancer?

7 07 2009

Last week my eyes were caught by a post of Kevin MD at his blog entitled

Does insulin cause cancer, and should you stop taking Lantus?”.

Kevin linked to the blog of Dr. Mintz, a board-certified internist, who had a strong opinion on this. Dr. Mintz  posted 3 blog articles on the matter, entitled: A new problem with insulin: cancer (June 29), Lantus causes cancer! Why doesn’t anyone seem to care? (July 1) and Lantus and cancer – A closer look is not reassuring (July 2). Dr. Mintz’s conclusion was based on 4 recent publications in diabetologica (1-4)6-7-2009 10-14-07 dr Mintz + foto

Alarming. Especially since Dr. Mintz is an expert, often prescribing insulins. Also, I’m suspicious  about any substance with an IGF (insulin growh factor)-like action, because I know from previous work in the lab that some tumor cells (i.e. prostate and breast cancer) thrive on IGF. On the other hand there have been several examples in the past, where retrospective studies initially “showed” drugs to cause cancer, which have later been invalidated by more thorough studies (i.e. statins).

“Lantus causing cancer” is a serious allegation, that might cause panic in those many diabetic patients using Lantus. Are fears justified and should Lantus be “banned”?

After reading the publications (1-5), news articles and some blogposts (i.e. a balanced blogpost at Diabetesmine, a blog of a patient) and a very thorough blogpost in Dutch), I rather conclude that the recent publications in Diabetologica, dr Mintz* refers to, do not support a causal role for Lantus in cancer. However, they still give reason for some serious concern in a subset of patients (explained below).

Now what is Lantus and what have preclinical and clinical trials revealed?

Insulin glargine (Lantus) is the first of the long-acting insulin analogues, introduced in 2001. This analogue is a so called designer molecule made by the recombinant DNA technique. It has three amino-acid substitutions, that cause a lower solubility of the insulin molecule  at the injection site, forming a depot from which insulin is slowly released (9, 10).  The advantage is that stable 24hr blood glucose concentrations are reached by a once daily subcutaneous injection without a blood glucose peak upon injection as seen with the short acting insulins. However, insulin replacement remains far from ‘natural’, “the insulin is injected in the wrong site (subcutaneously instead of intraportally), in shots (instead of a continuous low secretion associated with a prompt release in response to a meal, with a total lack of the physiological pulsatile secretion”).lantus pen + kineticsInsulins not only bind to the insulin receptor, leading to the intended glucose lowering, but also to the insulin growth factor receptor (IGF-R), which mainly induces cell proliferation. Importantly, glargine has a much higher affinity for both receptors than insulin. This can lead to a sustained activation of the IGF-receptor, resulting in enhanced cell growth.

Indeed, Preclinical Research has shown that only glargine showed a significantly higher proliferative effect on breast cancer cells compared to regular insulin among a panel of short- or long-acting insulin analogues (6) . Futhermore,  insulin analogues display IGF-I-like mitogenic and anti-apoptotic activities in cultured cancer cells (thus they stimulate cell division and prevent programmed cell death of cancer cells (8).

Experimental animal studies haven’t shown a tumorigenic or teratogenic potential of glargine, except for histiocytomas in male rat (Product information Lantus). Such studies don not examine tumor promoting properties (see below)

Clinical Studies (published in Diabetologica 2009)

Based on the insulin analogue characteristics and the in vitro results there was already concern about possible increased cancer risk of glargine. But the concern was boosted by a prominent diabetes researcher forecasting an “earthquake” event compromising the safety profile of Lantus,  and the subsequent publication of five studies in  the European journal Diabetologia, the Journal of the EASD (European Association for the of Study of Diabetes).

Except for one small study, which was a post-hoc analysis of a randomized study by Sanofi-Aventis itself [5], all other studies were retrospective. The Sanofi study didn’t find an increase in cancer, but given its small size (1000 patients), it is not  convincing enough to exclude a higher risk of cancer.

The first, German, study [1] was submitted a year ago, but because of the uncertainties and the expected high impact, researchers from other European countries were asked to replicate the findings before announcing them formally. Studies were carried out using databases from Sweden, Scotland, and the UK.

The German study (n= 127,031 patients, exclusively on human insulin or on one type of insulin analogues (lispro, aspart or glargine; glargine: n=23,855 ; mean follow-up time 1.63 years) found an overall increase in cancers, independent of the insulin used. After statistical modeling, a dose-dependent increase in cancer risk was found for treatment with glargine compared with human insulin (p<0.0001): with an adjusted HR of 1.31 (95% CI 1.20 to 1.42) for a daily dose of 50 IU, meaning that out of every 100 people who used Lantus insulin one additional person was diagnosed with cancer over the study period. The baseline characteristics were different between the groups. It was not possible to break the analysis down to type of cancer.

The Swedish and Scottish studies [2-3], both based on matching of national databases for cancer and diabetes, showed no overall increase in cancer, but an increased incidence rate of breast cancer in women using insulin glargine monotherapy (no other types of insulin or combination) as compared with women using types of insulin other than insulin glargine. Although this can be caused by chance, it is striking that both studies had a similar outcome. The enhanced risk was abolished in patients using glargine together with other insulins. These were mostly younger patients with diabetes type 1.

The fourth smaller study [4] found that patients on insulin were more likely to develop solid cancers than those on metformin, and combination with metformin abolished most of this excess risk. No harmful effect on cancer development, including breast cancer were observed: there was only a higher risk versus metformin, which has known anti-cancer properties.

In Conclusion:

  • Diabetes patients using insulin should never stop using insulin, as this is very dangerous.
  • Long term studies have shown ‘natural’ insulins to be effective and safe.
  • The reported studies do NOT show that Lantus can CAUSE cancer. Moreover, the time span (less than two years) is too short for any drug to cause cancer.
  • The enhanced risk was only observed for breast cancer (2-3) and/or if Lantus was used on its own, thus not with other insulins (1-3) or metformin (4). The association was clearest in type 2 diabetes patients. It is not clear whether the association reflects the effects of Lantus or the inherent differences between for instance diabetes I/younger  and diabetes II/older patients (also because the latter often use Lantus alone ). In addition, it should be noticed that diabetes patients already have a higher cancer risk (possibly related to overweight, often seen in type 2 diabetes)
  • At the most Lantus might promote existing cancer to grow and divide. Lantus might for instance provide a survival advantage of percancerous or cancerous cells. This would be consistent with its in vitro mitogenic effect on breast cancer cells.
  • On the basis of the current evidence there is no need to switch to other treatments when a long acting insulin is necessary to keep blood glucose under control. However, Lantus treatment could be reconsidered in diabetes II patients, with good control of blood glucose, for whom a clear benefit of Lantus has not been shown or  in patients with a higher cancer risk.
  • Levamir is considered as a good alternative by some, because this long acting insulin analogue lacks the greater affinity for IGF-R. However, absence of proof is no proof of absence: Levamir has only recently been introduced, it has not been included in these studies and clinical experience is limited.
  • More conclusive evidence is to be expected from analysis of the large combined analysis of the databases available worldwide, by EASD and sanofi-aventis. Results are expected within a few months.

Video-editorials featuring Prof. Ulf Smith, Director EASD, and Prof Edwin Gale, editor-in-chief Diabetologica (part 1 and 2)

*dr Mintz reformulated this in his last post, where he stated that “it is unlikely that Lantus actually causes cancer alone, because it takes years to develop most cancers. However, it is more likely that Lantus causes existing cells to grow and divide more rapidly.

Journal ArticlesResearchBlogging.org

  1. Hemkens, L., Grouven, U., Bender, R., Günster, C., Gutschmidt, S., Selke, G., & Sawicki, P. (2009). Risk of malignancies in patients with diabetes treated with human insulin or insulin analogues: a cohort study Diabetologia DOI: 10.1007/s00125-009-1418-4 (Free full text)
  2. Jonasson, J.M., Ljung, R, Talbäck, M, Haglund, B, Gudbjörnsdòttir, S, & Steineck, G (2009). Insulin glargine use and short-term incidence of malignancies—a population-based follow-up study in Sweden Diabetologia (Free full text)
  3. SDRN Epidemiology Group (2009). Use of insulin glargine and cancer incidence in Scotland: A study from the Scottish Diabetes Research Network Epidemiology Group Diabetologia (Free full text)
  4. Currie, C., Poole, C., & Gale, E. (2009). The influence of glucose-lowering therapies on cancer risk in type 2 diabetes Diabetologia DOI: 10.1007/s00125-009-1440-6 (Free full text)
  5. Smith, U., & Gale, E. A. M. (2009). Does diabetes therapy influence the risk of cancer? Diabetologia (Free full text)
  6. Mayer D, Shukla A, Enzmann H (2008) Proliferative effects of insulin analogues on mammary epithelial cells. Arch Physiol Biochem 114: 38-44
  7. Arch Physion Biochem (2008), vol 1141 (1) is entirely dedicated to “Insulin and Cancer”, i.e. see editorial of P. Lefèbvre: Insulin and cancer: Should one worry?” p. 1-2
  8. Weinstein D, Simon M, Yehezkel E, Laron Z, Werner H (2009) Insulin analogues display IGF-I-like mitogenic and anti-apoptotic activities in cultured cancer cells. Diabetes Metab Res Rev 25: 41-49 (PubMed record)

Information about Lantus

9.  http://content.nejm.org/cgi/content/extract/352/2/174

10. http://products.sanofi-aventis.us/lantus/lantus.html

11. http://www.informapharmascience.com/doi/abs/10.1517/14656566.2.11.1891?journalCode=eop





Some Sugars Worse than Others? The Bittersweet Fructose/Glucose Debate.

27 04 2009

132244825_dbf0e21d9fExcessive consumption of sugar has been associated with increased incidences of type 2 diabetes, formerly called adult-onset diabetes, obesity and tooth decay.

There are many sugars around. Natural sugars and refined sugars. The refined table sugar and sugar cubes would be called “sucrose” by a chemist. Sucrose consists of two simple sugars (monosaccharides): 1 fructose and 1 glucose molecule (5).

542compareglufrucGlucose is a sugar that occurs in the blood. Because of its name, fructose (Latin= fructus, fruit) is often regarded as more “natural” and therefore as a healthier alternative to glucose. However, unlike glucose, that can be metabolized anywhere in the body, fructose has to be metabolized by the liver. Here, fructose is easily converted to fat.

There is an intensive debate whether glucose or fructose is the real culprit for overweight and related health problems. This discussion is  relevant, because of the shift towards use of (cheaper) high fructose corn syrup from sucrose (especially in the US).

Last week a journal article was published in the Journal of Clinical Investigation, written by Stanhope et al (1) that was widely covered in the media. Headlines were for instance “Fructose slechter dan glucose” (NRC, Dutch, 8), “Fructose is the bad sugar, not glucose” (Indo-Asian News Service, i.e. 9) “Fructose-Sweetened Beverages Linked to Heart Risks” (NY-times, 10).

Is this study a breakthrough? What has been done?

This study was a double-blinded parallel arm study that assessed the relative effects of fructose- versus glucose – sweetened beverages in 32 matched, obese individuals, 40 to 72 years old (see 1).

The study consisted of 3 phases:

  1. The first 2 weeks the volunteers lived in a clinical research center, consuming an energy- balanced high complex carbohydrate diet. This phase established baseline measurements for the study.
  2. An 8-week outpatient intervention period during which subjects consumed either fructose- or glucose-sweetened beverages providing 25% of daily energy requirements along with their usual ad libitum diet. The aim was to imitate the ‘normal situation’, where sugar-sweetened beverages are typically consumed as part a normal energy-rich diet.
  3. A 2-week inpatient intervention period during which subjects consumed fructose- or glucose-sweetened beverages providing 25% of daily energy requirements with an energy-balanced diet.

Results

Both study groups put on the same amount of weight, but people drinking fructose showed an increase in intra-abdominal fat, an increased hepatic de-novo (new) synthesis of lipids, higher triglyceride, LDL and oxidized LDL (“bad fats”), and higher fasting plasma glucose and insulin levels, but lowered insulin sensitivity. All these parameters are associated with a higher risk for diabetes and cardiovascular disease.

Positive Aspects of the study

  • Intervention directly comparing fructose and glucose
  • Human study
  • Randomized Controlled Trial
  • Many variables measured, related to diabetes and cardiovascular disease.

Critique:

  • The first thing that came to my mind was: is it ethical to expose obese man and woman (or any healthy volunteer) to 10 weeks of a very unhealthy diet: extra glucose or fructose beverages making up 25% of the calorie intake?
  • Because the subjects were obese, the results may not directly apply to lean persons.
  • Minor point: It is a rather difficult to read paper, with a plethora of data. I wonder why SEM are given instead of SD and why the statistical significance is only determined versus baseline.
  • Only surrogate markers were tested.
  • Most important: the doses of sugars used are excessive, not reflecting a real-life diet.
  • Nor can results with pure fructose be directly translated to health effects of high-fructose corn syrup, which is not pure fructose, but still contains 45% glucose.
  • In addition the abstract and introduction suggests that it is the first human intervention study, which it isn’t.

Quite coincidentally the Journal of Nutrition published a supplement about “the State of the Science on Dietary Sweeteners Containing Fructose” [2-4]. In his paper Geoffrey Livesey [2] stresses the pitfalls of studies on Fructose, not only of animal and epidemiological studies, but also of intervention studies using excessive high fructose (excessive is > 400 kcal/day = >20% of energy intake), that may bear little relevance to the normal situation.

Many hypotheses of disease risk and prevention depend on inferences about the metabolic effects of fructose; however, there is inadequate attention to dose dependency. Fructose is proving to have bidirectional effects. At moderate or high doses, an effect on any one marker may be absent or even the opposite of that observed at very high or excessive doses; examples include fasting plasma triglyceride, insulin sensitivity (..) Among markers, changes can be beneficial for some (..) but adverse for others (e.g., plasma triglycerides at very high or excessive fructose intake). Evidence on body weight indicates no effect of moderate to high fructose intakes, but information is scarce for high or excessive intakes. The overall balance of such beneficial and adverse effects of fructose is difficult to assess but has important implications for the strength and direction of hypotheses about public health, the relevance of some animal studies, and the interpretation of both interventional and epidemiological studies.

3198244845_76f72e7966

References:

  1. ResearchBlogging.orgStanhope, K., Schwarz, J., Keim, N., Griffen, S., Bremer, A., Graham, J., Hatcher, B., Cox, C., Dyachenko, A., Zhang, W., McGahan, J., Seibert, A., Krauss, R., Chiu, S., Schaefer, E., Ai, M., Otokozawa, S., Nakajima, K., Nakano, T., Beysen, C., Hellerstein, M., Berglund, L., & Havel, P. (2009). Consuming fructose-sweetened, not glucose-sweetened, beverages increases visceral adiposity and lipids and decreases insulin sensitivity in overweight/obese humans Journal of Clinical Investigation DOI: 10.1172/JCI37385
  2. Livesey, G. (2009). Fructose Ingestion: Dose-Dependent Responses in Health Research Journal of Nutrition DOI: 10.3945/jn.108.097949
  3. White, J. (2009). Misconceptions about High-Fructose Corn Syrup: Is It Uniquely Responsible for Obesity, Reactive Dicarbonyl Compounds, and Advanced Glycation Endproducts? Journal of Nutrition DOI: 10.3945/jn.108.097998
  4. Jones, J. (2009). Dietary Sweeteners Containing Fructose: Overview of a Workshop on the State of the Science Journal of Nutrition DOI: 10.3945/jn.108.097972
  5. Wikipedia: http://en.wikipedia.org/wiki/Sugar
  6. Essentially Healthy Food: Sugar, a bittersweet story part 2
  7. http://www.askmen.com/sports/foodcourt_250/257_health-benefits-of-sugar.html
  8. NRC, April 21, 2009. http://www.nrc.nl/wetenschap/article2219138.ece/Fructose_slechter_dan_glucose
  9. The Idian http://www.thaindian.com/newsportal/sci-tech/fructose-is-the-bad-sugar-not-glucose_100184408.html
  10. NY Times,  April 2, 2009: Fructose-Sweetened Beverages Linked to Heart Risks

Photo Credits





Still Confusion about the Usefulness of PSA-screening.

13 04 2009

Prostate cancer is the most commonly diagnosed cancer affecting older men and second-biggest cancer killer. pc_epid_fig11a

Prostate Specific Antigen (PSA), a protein mainly produced by the prostate gland, is often elevated in prostate cancer – and often proportional to the prostate cancer volume. Since more men are diagnosed with prostate cancer by using PSA screening, middle-aged men have been advised to undergo a simple blood test to determine their blood PSA levels.

Indeed in the 20 years that the PSA test has been used there has been a significant drop in prostate cancer deaths.

However, this may have also resulted from better treatment modalities.

Furthermore, PSA tests are prone to false negative results (prostate cancer present in the complete absence of an elevated PSA level ), or vice versa, false positive results: elevated PSA occurring in non-cancerous prostate diseases, like prostate infection and benign prostatic hyperplasia (BPH). Some detected prostate cancers may also be indolent, never giving any trouble on the long term. Since the further diagnosis methods (biopsy) and treatment methods (irradiation, surgery, hormonal treatment) often have serious side effects (erectile dysfunction, urinary incontinence and bowel problems), there is a clear need to demonstrate whether PSA screening is worth the high risks of overdiagnosis and overtreatment:

Thus, does PSA screening really saves lives?
And what is the trade off between benefits and harms?

A Cochrane Systematic Review from 2006 [5] (also reviewed in EBM-online) concluded that there was no proof of benefit of PSA-screening. Yet absence of proof is not proof of absence. Moreover, both trials on which the review was based had methodological weaknesses.
Therefore, the main conclusion was to wait for the results from two large scale ongoing randomized controlled trials (RCTs).

The first study results of these two large RCT’s,  that many observers hoped would settle the controversy, have appeared in the March issue of the New England Journal of Medicine (NEJM). [1,2] The results are discussed in an accompanying editorial [3] and in a Perspective Roundtable [4] (with a video).

It should be stressed, however, that these are just interim results.

One of these two studies [1], the prostate component of the U.S. National Cancer Institute’s Prostate, Lung, Colorectal, and Ovarian Cancer Screening Trial (PLCO) showed no prostate specific mortality reduction over 11 yrs follow-up in 76,705 men by annual PSA screening and DRE (digital rectal exam). However:

  • The cut off is relatively high (4.0 ng per milliliter), which means that some prostate cancers could have been missed (on the other hand lowering the screening criteria might also have led to a higher false negative response)
  • The control group is “highly contaminated”, meaning that many men in the so called nonscreened arm had a PSA-test anyway ((52% in the nonscreened versus 85% in the screened arm).
  • The 11 yr follow up may be too short to show any significant effect. “Only” 0,1% of the men died of prostate cancer. On the long term the differences might become larger.
  • Since there were only 122 prostate cancer deaths in the screening group versus 135 in the control group, the power of the study to find any differences is mortality seems to be rather low.

The European ERSPC study [2] is larger than the PLCO trial (190,000 men), the cut off rate was lower (3.0 µg/L), and there was less contamination of the nonscreened arm. A shortcoming of the trial is that the diagnosis methods varied widely among centers participating in the trial. The follow-up time is 9 years.

The ESPRC trial noticed a difference in mortality between the screened and non-screened arms. Surprisingly the same outcome led to widely different conclusions, especially in the media (see Ben Goldacre on his blog Bad Science [6])

English newspapers concluded that the ERPSC study showed a clear advantage: Prostate cancer screening could cut deaths by 20% said the Guardian. Better cancer screening is every man’s right was the editorial in the Scotsman (see 6). These newspapers didn’t mention the lack of effect in the US study.

But most US newspapers, and scientists, concluded that the benefits didn’t outweigh the risks.

Why this different interpretation?

It is because 20% is the relative risk reduction. This means that the risk of getting prostate cancer is reduced by 20%. This sounds more impressive than it is, because it depends on your baseline risk. It is the absolute reduction that counts.
Suppose you would have a baseline chance of 10% of getting prostate cancer. Reducing this risk by 20% means that the risk is reduced from 10% to 8%. This sounds a lot less impressive.
But in reality your chance of getting prostate cancer comes closer to 0,1%. Then, a risk reduction of 20% becomes even less significant: it means your risk has decreased to 0,08%.

Absolute numbers are more meaningful. In the ESPRC trial[2], the estimated absolute reduction in prostate-cancer mortality was about 7 deaths per 10,000 men after 9 years of follow-up. This is not a tremendous effect. However the costs are high: to prevent one death from prostate cancer 1410 men would need to be screened and 48 additional cases of prostate cancer would need to be treated.

Overdiagnosis and overtreatment are probably the most important adverse effects of prostate-cancer screening and are vastly more common than in screening for breast, colorectal, or cervical cancer.

It is difficult to realize the impact of a false negative diagnosis. People tend to think that saving any live is worth any cost. But that isn’t the case.

This quote says a lot (from Ray Sahelian)

A few years ago my dad was found to have a high PSA test. He was 74 at the time. He underwent multiple visits to the doctor over the next few months with repeated PSA tests and exams, and eventually a biopsy indicated he had a small prostate cancer. I remember my dad calling me several times a month during that period constantly asking my thoughts on how he should proceed with radiation or other treatments for his cancer. My dad had a preexisting heart condition known as atrial fibrillation. I suggested he not undergo any treatment for the small cancer but just to follow the PSA levels. His doctor had agreed with my opinion. His PSA test stayed relatively the same over the next few years and the prostate cancer did not grow larger. My dad died at 78 from a heart rhythm problem. Ever since the discovery of the high PSA level, he was constantly worried about this prostate gland. What good did it do to have this PSA test at his age? It only led to more doctor visits, a painful prostate gland biopsy, and constant worry. Maybe the constant worry even made his heart weaker.

Indeed more men die with prostate cancer than of it.It’s estimated that appr 30% of American men over age 60 have small, harmless prostate cancers.

Although still hypothetical, non-invasive tests that would discriminate between low- and high risk prostate cancer could be a real solution to the problem. One such candidate might be the recently discovered urine test for sarcosine [7]

In conclusion
PSA-screening is associated with an earlier diagnosis of prostate cancer, but the present evidence shows at the most a slight reduction in prostate related mortality. Since screening and subsequent testing do have serious side effects, there seems a trade off between uncertain benefits and known harms. However, definite conclusions can only be drawn after complete follow-up and analyses of these and other studies [1,2,3]

REFERENCES

  1. ResearchBlogging.orgAndriole, G., Grubb, R., Buys, S., Chia, D., Church, T., Fouad, M., Gelmann, E., Kvale, P., Reding, D., Weissfeld, J., Yokochi, L., Crawford, E., O’Brien, B., Clapp, J., Rathmell, J., Riley, T., Hayes, R., Kramer, B., Izmirlian, G., Miller, A., Pinsky, P., Prorok, P., Gohagan, J., Berg, C., & , . (2009). Mortality Results from a Randomized Prostate-Cancer Screening Trial New England Journal of Medicine DOI: 10.1056/NEJMoa0810696
  2. Schroder, F., Hugosson, J., Roobol, M., Tammela, T., Ciatto, S., Nelen, V., Kwiatkowski, M., Lujan, M., Lilja, H., Zappa, M., Denis, L., Recker, F., Berenguer, A., Maattanen, L., Bangma, C., Aus, G., Villers, A., Rebillard, X., van der Kwast, T., Blijenberg, B., Moss, S., de Koning, H., Auvinen, A., & , . (2009). Screening and Prostate-Cancer Mortality in a Randomized European Study New England Journal of Medicine DOI: 10.1056/NEJMoa0810084
  3. Barry, M. (2009). Screening for Prostate Cancer — The Controversy That Refuses to Die New England Journal of Medicine, 360 (13), 1351-1354 DOI: 10.1056/NEJMe0901166
  4. Lee, T., Kantoff, P., & McNaughton-Collins, M. (2009). Screening for Prostate Cancer New England Journal of Medicine, 360 (13) DOI: 10.1056/NEJMp0901825
  5. Ilic D, O’Connor D, Green S, Wilt T. Screening for prostate cancer. Cochrane Database Syst Rev. 2006;3:CD004720.[Medline]
  6. Goldacre, Ben (2009) Bad Science: Venal-misleading-pathetic-dangerous-stupid-and-now-busted.net. (2009/03/), also Published in The Guardian, 21 March 2009
  7. Sreekumar A et al. (2009) Metabolomic profiles delineate potential role for sarcosine in prostate cancer progression Nature 457 (7231): 910-914 DOI: 10.1038/nature07762




An Antibiotic Past May Save Lives at the ICU.

16 03 2009

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Respiratory tract infections acquired in the intensive care unit (ICU) are important causes of morbidity and mortality, the most significant risk factor being mechanical ventilation. It is thought that hospital pneumonia commonly originates from flora colonized in the patient’s oropharynx (the area of the throat at the back of the mouth). Therefore, reduction of respiratory tract infections has been obtained by putting patients in semirecumbent instead of supine position. Another approach is selective decontamination. There are two methods of selective decontamination, SDD and SOD.

  1. SDD, Selective Decontamination of the Digestive tract consists of the administration of topical nonabsorbable antibiotics in the oropharynx and gastrointestinal tract, often concomitant with systemic antibiotics. It aims to reduce the incidence of pneumonia in critically ill patients by diminishing colonization of the upper respiratory tract with aerobic gram-negative bacilli and yeasts, without disrupting the anaerobic flora.
  2. SOD, Selective Oropharyngeal Decontamination is application of local antibiotics in the oopharynx only.

Both approaches were first introduced in the Netherlands. Most trials suggested that SDD lowered infection rates, but lacked statistical power to demonstrate an effect on mortality. However, meta-analyses and three single-center, randomized studies, did show a survival benefit of SDD in critically ill patients. Several studies had suggested that the local variant, SOD, was also effective, but SOD was never directly compared with SDD in the same study. Because of methodological issues and concern about increasing antibiotic resistance the use of both SDD and SOD has remained controversial. Even in the Netherlands where guidelines recommended the use of SDD after a Dutch publication in the Lancet (de Jonge et al, 2003) had shown the mortality to drop with 30% in the Academic Medical Center in Amsterdam, only 25% of the emergency doctors followed the guidelines.

The present Dutch study, published in the NEJM (2009), was undertaken to determine the effects on mortality in a head to head comparison of SDD and SOD. The effectiveness of SDD and SOD was determined in a crossover study using cluster randomization in 13 Dutch ICU’s, differing in size and teaching status. Cluster randomization means that ICU’s rather than the individual patients were randomized to avoid that one treatment regimen would influence the outcome of another regimen. Crossover implies that all three treatments (SDD, SOD, standard care) were administered in a random order in all ICU’s.

A total of 5939 patients were enrolled in this large study. Patients were eligible if they were expected to be intubated for more than 48 hours or to stay in the ICU for more than 72 hours. The SDD regimen involved four days of intravenous cefotaxime along with topical application of tobramycin, colistin and amphotericin B; the SOD regimen used only the topical antibiotics. Both regimens were compared with standard care. The duration of the study was six months, and the primary end point was 28-day mortality.

Of the 5,939 patients, 1,990 received standard care, 1,904 received SOD and 2,405 received SDD. Crude mortality rates in the three groups were 27.5%, 26.6% and 26.9%, respectively. These differences are not very huge and benefit was only discernable after adjustment for covariates (age, sex, APACHE II score, intubation status, medical specialty, study site, and study period): adjusted* odds ratios for 28-day mortality were 0.86 (95% CI, 0.74 to 0.99) in the SOD group and 0.83 (95% CI, 0.72 to 0.97) in the SDD group compared with standard care. This corresponded with the needed-to-treat numbers (NNT’s) of 29 and 34 to prevent one casualty at day 28 for SDD and SOD, respectively.

The limitations of the study (acknowledged by the authors) were the absence of concealment of allocation (due to the study design it was impossible to conceal the allocation for doctors at the wards), differences at baseline between the standard care and treatment groups and a mismatch between the original analysis plan and the study design (originally specified in-hospital death was the primary end point, but this did not take into account analysis of cluster effects.)

Selective Decontamination also improved microbiological outcomes, such as carriage of gram-negative bacteria in the respiratory and intestinal tracts and ICU-acquired bacteriemia. During the study periods the prevalence rates for antibiotic-resistant gram-negative bacteria were lower in the SOD and SDD periods than during the standard-care periods.

The authors concluded that both SDD and SOD were effective compared with standard care. Given the similarity in effects on survival between the treatment groups, the SOD regimen seems preferable to the SDD regimen, becauses it minimizes the risk of antibiotic resistance which poses a major threat to patients admitted to ICU’s. It should be noted that MRSA-infections are very rare in the Netherlands and in Scandinavia. The outcome of the study might therefore be different after long term treatment and/or in regions with a high prevalence of MRSA.

References

ResearchBlogging.orgde Smet, A., Kluytmans, J., Cooper, B., Mascini, E., Benus, R., van der Werf, T., van der Hoeven, J., Pickkers, P., Bogaers-Hofman, D., van der Meer, N., Bernards, A., Kuijper, E., Joore, J., Leverstein-van Hall, M., Bindels, A., Jansz, A., Wesselink, R., de Jongh, B., Dennesen, P., van Asselt, G., te Velde, L., Frenay, I., Kaasjager, K., Bosch, F., van Iterson, M., Thijsen, S., Kluge, G., Pauw, W., de Vries, J., Kaan, J., Arends, J., Aarts, L., Sturm, P., Harinck, H., Voss, A., Uijtendaal, E., Blok, H., Thieme Groen, E., Pouw, M., Kalkman, C., & Bonten, M. (2009). Decontamination of the Digestive Tract and Oropharynx in ICU Patients New England Journal of Medicine, 360 (1), 20-31 DOI: 10.1056/NEJMoa0800394

de Jonge E, Schultz M, Spanjaard L, et al. Effects of selective decontamination of the digestive tract on mortality and acquisition of resistant bacteria in intensive care: a randomised controlled trial. Lancet 2003;362:1011-1016 (PubMed citation)

Wim Köhler (2009) Smeren tegen infectie, NRC Handelsblad, Wetenschapsbijlage 3,4 januari (Dutch, online)

Barclay, L & Vega, C (2009) Selective Digestive, Oropharyngeal Decontamination May Reduce Intensive Care Mortality, Medscape

File, T.M., Bartlett J.G.,& Thorner, A.R. Risk factors and prevention of hospital-acquired (nosocomial); ventilator-associated; and healthcare-associated pneumonia in adults.www.uptodate)

Photo Credit (CC): http://www.flickr.com/photos/30688696@N00/3241003338/ (JomCleay)





Yet Another Negative Trial with Vitamins in Prostate Cancer: Vitamins C and E.

15 12 2008

Within a week after the large SELECT (Selenium and Vitamin E Cancer Prevention) Trial was halted due to disappointing results (see previous posts: [1] and [2]), the negative results of yet another large vitamin trial were announced [7].
Again, no benefits were found from either vitamin C or E when it came to preventing prostate ànd other cancers.
Both trials are now prepublished in JAMA. The full text articles and the accompanying editorial are freely available [3, 4, 5].

In The Physicians’ Health Study II Randomized Controlled Trial (PHS II), researchers tested the impact of regular vitamin E and C supplements on cancer rates among 14,641 male physicians over 50: 7641 men from the PHS I study and 7000 new physicians.

The man were randomly assigned to receive vitamin E, vitamin C, or a placebo. Besides vitamin C or E, beta carotene and/or multivitamins were also tested, but beta carotene was terminated on schedule in 2003 and the multivitamin component is continuing at the recommendation of the data and safety monitoring committee.

Similar to the SELECT trial this RCT had a factorial (2×2) design with respect to the vitamins E and C [1]: randomization yielded 4 nearly equal-sized groups receiving:

  • 400-IU synthetic {alpha}-tocopherol (vitamin E), every other day and placebo (similar to the SELECT trial)
  • 500-mg synthetic ascorbic acid (vitamin C), daily and placebo
  • both active agents
  • both placebos.

Over 8 years, taking vitamin E had no impact at all on rates of either prostate cancer (the primary outcome for vitamin E), or cancer in general. Vitamin C had no significant effect on total cancer (primary outcome for vitamin C) and prostate cancer. Neither was there an effect of vitamin E and/or C on other site-specific cancers.

How can the negative results be explained in the light of the positive results of earlier trials?

  • The conditions may differ from the positive trials:
    • The earlier positive trials had less methodological rigor. These were either observational studies or prostate cancer was not their primary outcome (and may therefore be due to chance). (See previous post The best study design for dummies).
    • Clinical data suggest that the positive effect of vitamin E observed in earlier trials was limited to smokers and/or people with low basal levels of vitamin E, whereas animal models suggest that vitamin E is efficacious against high fat-promoted prostate cancer growth (20), but lacks chemopreventive effects (i.e. see [1,4] and references in [5], a preclinical study we published in 2006).
      Indeed, there were very low levels of smoking in the PHS II study and the effect of the vitamins was mainly assessed on induction not on progression of prostate cancer.
    • Eight times higher vitamin E doses (400IE) have been used than in the ATCB study showing a benefit for vitamin E in decreasing prostate cancer risk! [1,4]
  • Other forms of vitamin E and selenium have been proposed to be more effective.
  • As Gann noted in the JAMA-editorial, the men in both recent studies were highly motivated and had good access to care. In SELECT, the majority of men were tested for PSA each year. Probably because of this intense surveillance, the mean PSA at diagnosis was low and prostate cancers were detected in an early, curable stage. Strikingly, there was only 1 death from prostate cancer in SELECT, whereas appr. 75-100 deaths were expected. There also were indications of a deficit in advanced prostate cancer in PHS II, although a much smaller one.
    In other words (Gann):
    “how can an agent be shown to prevent serious, clinically significant prostate cancers when PSA testing may be rapidly removing those cancers from the population at risk before they progress?”
  • Similarly, in the SELECT trial there was no constraint on the use of other multivitamins and both studies put no restriction on the diet. Indeed the group of physicians who participated in the PHS II trial were healthier overall and ate a more nutritious diet. Therefore Dr Shao wondered
    “Do we really have a placebo group – people with zero exposure? None of these physicians had zero vitamin C and E” [7]. In the Netherlands we were not even able to perform a small phase II trial with certain nutrients for the simple reason that most people already took them.

What can we learn from these negative trials (the SELECT trial and this PHS II-trial)?

  • Previous positive results were probably due to chance. In the future a better preselection of compounds and doses in Phase 2 trials should determine which few interventions make it through the pipeline (Gann, Schroder).
  • Many other trials disprove the health benefits of high dose vitamins and some single vitamins may even increase risks for specific cancers, heart disease or mortality [9]. In addition vitamin C has recently been shown to interfere with cancer treatment [10].
  • The trials make it highly unlikely that vitamins prevent the development of prostate cancer (or other cancers) when given as a single nutrient intervention. Instead, as Dr Sasso puts it “At the end of the day this serves as a reminder that we should get back to basics: keeping your body weight in check, being physically active, not smoking and following a good diet.”
  • Single vitamins or high dose vitamins/antioxidants should not be advised to prevent prostate cancer (or any other cancer). Still it is very difficult to convince people not taking supplements.
  • Another issue is that all kind of pharmaceutical companies keep on pushing the sales of these “natural products”, selectively referring to positive results only. It is about time to regulate this.

1937004448_dfcf7d149f-vitamines-op-een-bordje1

Sources & other reading (click on grey)

  1. Huge disappointment: Selenium and Vitamin E fail to Prevent Prostate Cancer.(post on this blog about the SELECT trial)
  2. Podcasts: Cochrane Library and MedlinePlus: (post on this blog)
  3. Vitamins E and C in the Prevention of Prostate and Total Cancer in Men: The Physicians’ Health Study II Randomized Controlled Trial. J. Michael Gaziano et al JAMA. 2008;0(2008):2008862-11.[free full text]
  4. Effect of Selenium and Vitamin E on Risk of Prostate Cancer and Other Cancers: The Selenium and Vitamin E Cancer Prevention Trial. Scott M. Lippman, Eric A. Klein et al (SELECT)JAMA. 2008;0(2008):2008864-13 [free full text].
  5. Randomized Trials of Antioxidant Supplementation for Cancer Prevention: First Bias, Now Chance-Next, Cause. Peter H. Gann JAMA. 2008;0(2008):2008863-2 [free full text].
  6. Combined lycopene and vitamin E treatment suppresses the growth of PC-346C human prostate cancer cells in nude mice. Limpens J, Schröder FH, et al. J Nutr. 2006 May;136(5):1287-93 [free full text].

    News
  7. The New York Times (2008/11/19) Study: Vitamins E and C Fail to Prevent Cancer in Men.
  8. BBC news: (2008/12/10) Vitamins ‘do not cut cancer risk’.
  9. The New York Times (2008/11/20) News keeps getting worse for vitamins.
  10. The New York Times (2008/10/01) Vitamin C may interfere with cancer treatment.











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