OK, I admit that I pulled a fast one. I never finished the last post as promised, so here it is.

Cochrane Continued

In the last post I alluded to the 2006 Cochrane Laetrile review, the conclusion of which was:

This systematic review has clearly identified the need for randomised or controlled clinical trials assessing the effectiveness of Laetrile or amygdalin for cancer treatment.

I’d previously asserted that this conclusion “stand[s] the rationale for RCTs on its head,” because a rigorous, disconfirming case series had long ago put the matter to rest. Later I reported that Edzard Ernst, one of the Cochrane authors, had changed his mind, writing, “Would I argue for more Laetrile studies? NO.” That in itself is a reason for optimism, but Dr. Ernst is such an exception among “CAM” researchers that it almost seemed not to count.

Until recently, however, I’d only seen the abstract of the Cochrane Laetrile review. Now I’ve read the entire review, and there’s a very pleasant surprise in it (Professor Simon, take notice). In a section labeled “Feedback” is this letter from another Cochrane reviewer, which was apparently added in August of 2006, well before I voiced my own objections:

The authors’ state that they: “[have] clearly identified the need for randomised or controlled clinical trials assessing the effectiveness of Laetrile or amygdalin for cancer treatment.” This is to fail completely to understand the nature of oncology research in which agents are tested in randomized trials (“Phase III”) only after they have been successful in Phase I and II study. There was a large Phase II study of laetrile (N Engl J Med. 1982 Jan 28;306(4):201-6) which the authors of the review do not cite, they merely exclude as being non-randomized. But the results of the paper are quite clear: there was no evidence that laetrile had any effect on cancer (all patients had progression of disease within a few months); moreover, toxicity was reported. To expose patients to a toxic agent that did not show promising results in a single arm study is clinical, scientific and ethical nonsense.

I would like to make a serious recommendation to the Cochrane Cancer group that no reviews on cancer are published unless at least one of the authors either has a clinical practice that focuses on cancer or actively conducts primary research on cancer. My recollection when the Cochrane collaboration was established was that the combination of “methodologic” and “content” expertise was essential.

Wow! That letter makes several of the same arguments that we’ve made here: that for both scientific and ethical reasons, scientific promise (including success in earlier trials) ought to be a necessary pre-requisite for a large RCT; that the 1982 Moertel case series was sufficient to disqualify Laetrile; and that EBM, at least in this Cochrane review, suffers from “methodolatry.” It also brings to mind Steven Goodman’s words:

An important problem exists in the interpretation of modern medical research data: Biological understanding and previous research play little formal role in the interpretation of quantitative results. This phenomenon is manifest in the discussion sections of research articles and ultimately can affect the reliability of conclusions. The standard statistical approach has created this situation by promoting the illusion that conclusions can be produced with certain “error rates,” without consideration of information from outside the experiment.

…

This method thus facilitated a subtle change in the balance of medical authority from those with knowledge of the biological basis of medicine toward those with knowledge of quantitative methods, or toward the quantitative results alone, as though the numbers somehow spoke for themselves.

Perhaps most surprising about the ‘Feedback’ letter is the identity of its author: Andrew Vickers, a biostatistician who wrote the Center for Evidence-Based Medicine’s “Introduction to evidence-based complementary medicine.” I’ve complained about that treatise before in this long series, observing that

There is not a mention of established knowledge in it, although there are references to several claims, including homeopathy, that are refuted by things that we already know.

Well, Dr. Vickers may not have considered plausibility when he wrote his Intro to EBCM, but he certainly seems to have done so when he wrote his objection to the Cochrane Laetrile review. Which is an appropriate segue to a topic that Dr. Vickers hints at (“content expertise”), perhaps unintentionally, in the letter quoted above: Bayesian inference.

Bayes Revisited

A few years ago I posted three essays about Bayesian inference: they are linked below (nos. 2-4). The salient points are these:

1. Bayes’s Theorem is the solution to the problem of inductive inference, which is how medical research (and most science) proceeds: we want to know the probability of our hypothesis being true given the data generated by the experiment in question.
2. Frequentist inference, which is typically used for medical research, applies to deductive reasoning: it tells us the probability of a set of data given the truth of a hypothesis. To use it to judge the probability of the truth of that hypothesis given a set of data is illogical: the fallacy of the transposed conditional.
3. Frequentist inference, furthermore, is based on assumptions that defy reality: that there have been an infinite number of identically designed, randomized experiments (or other sort of random sampling), without error or bias.
4. Bayes’s Theorem formally incorporates, in its “prior probability” term, information other than the results of the experiment. This is the sticking point for many in the EBM crowd: they consider prior probability estimates, which are at least partially subjective, to be arbitrary, capricious, untrustworthy, and—paradoxically, because it is science that is ignored in the breach—unscientific.
5. Nevertheless, prior probability matters whether we like it or not, and whether we can estimate it with any certainty or not. If the prior probability is high, even modest experimental evidence supporting a new hypothesis deserves to be taken seriously; if it is low, the experimental evidence must be correspondingly robust to warrant taking the hypothesis seriously. If the prior probability is infinitesimal, the experimental evidence must approach infinity to warrant taking the hypothesis seriously. 
6. Frequentist methods lack a formal measure of prior probability, which contributes to the seductive but erroneous belief that “conclusions can be produced…without consideration of information from outside the experiment.”
7. The Bayes Factor is a term in the theorem that is based entirely on data, and is thus an objective measure of experimental evidence. Bayes factors, in the words of Dr. Goodman, “show that P values greatly overstate the evidence against the null hypothesis.”

I bring up Bayes again to respond to Prof. Simon’s statements, recently echoed by several readers, that people may differ strongly in what they consider plausible, and that it is not clear how prior probability estimates might be incorporated into formal reviews. I’ve discussed these issues previously (here and here, and in recent comments here and here), but it is worth adding a point or two.

First, it doesn’t really matter that people may differ strongly in what they consider plausible. What matters is that they commit to some range of plausibility—in public and with justifications, in the cases of authors and reviewers, so that readers will know where they stand—and that everyone understands that this matters when it comes to judging the experimental evidence for or against a hypothesis.

An example will explain these points. Wayne Jonas was the Director of the US Office of Alternative Medicine from 1995 until its metamorphosis into the NCCAM in 1999. He is the co-author, along with Jennifer Jacobs, of Healing with Homeopathy: the Doctors’ Guide (©1996), which unambiguously asserts that ultra-dilute homeopathic preparations have specific effects. Yet Jonas is also the co-author (with Klaus Linde) of a 2005 letter to the Lancet that includes this statement, prefacing his argument that homeopathy, already subjected to hundreds of clinical trials, has not been disproved and deserves further trials:

We agree that homoeopathy is highly implausible and that the evidence from placebo-controlled trials is not robust.

Bayes’s theorem shows that Jonas can’t have it both ways. Either he doesn’t really agree that homeopathy is highly implausible (which seems likely, unless he changed his mind between 1996 and 2005—oops, he didn’t); or, if he does, he needs to recognize that his statement quoted above is equivalent to arguing that the homeopathy ‘hypothesis’ has been disproved, at least to an extent sufficient to discourage further trials. 

Next, does it matter that we can’t translate qualitative statements of plausibility to precise quantitative measures? Does this mean that prior probability, in the Bayesian sense, is not applicable? I don’t think so, and neither do many scientists and statisticians. Even “neutral” or “non-informative” priors, when combined with Bayes factors, are more useful than P values (see #7 above). “Informative” priors—estimated priors or ranges of priors based on existing knowledge—are both useful and revealing: useful because they show how differing priors affect the extent to which we ought to revise our view of a hypothesis in the face of new experimental evidence (see #5 above); and revealing of where authors and others really stand, and of the information that those authors have used to make their estimates.

I believe that frequentist statistics has allowed Dr. Jonas and other “CAM” enthusiasts to project a posture of scientific skepticism, as illustrated by Jonas’s own words quoted above, without having to accept the consequences thereof. If convention had compelled him to offer a prior high enough to warrant further trials of homeopathy, Dr. Jonas would have revealed himself as credulous and foolish.

Finally, there is no reason that qualitative priors can’t be translated, if not precisely then at least usefully, to estimated quantitative priors. Sander Greenland, an epidemiologist and a Bayesian, explains this in regard to household wiring as a possible risk factor for childhood leukemia. First, he argues that there are often empirical bases for estimating priors:

…assuming (an) absence of prior information is empirically absurd. Prior information of zero implies that a relative risk of (say) 10¹⁰⁰ is as plausible as a value of 1 or 2. Suppose the relative risk was truly 10¹⁰⁰; then every child exposed >3 mG would have contracted leukaemia, making exposure a sufficient cause. The resulting epidemic would have come to everyone’s attention long before the above study was done because the leukaemia rate would have reached the prevalence of high exposure, or ~5/100 annually in the US, as opposed to the actual value of 4 per 100,000 annually; the same could be said of any relative risk >100. Thus there are ample background data to rule out such extreme relative risks.

The same could be said for many “CAM” methods that, while not strictly subjects of epidemiology per se, have generated ample experimental data (see homeopathy) or have been in use by enough people for enough time to have been noticed for substantial deviations from typical outcomes of universal diseases, should such deviations exist (see “Traditional [insert ethnic group here] Medicine”).

Next, Greenland has no problem with non-empirically generated priors, because these are revealing as well:

Many authors have expressed extreme scepticism over the existence of an actual magnetic-field effect, so much so that they have misinterpreted positive findings as null because they were not ‘statistically significant’ (e.g. UKCCS, 1999). The Bayesian framework allows this sort of prejudice to be displayed explicitly in the prior, rather than forcing it into misinterpretation of the data.

By “misinterpretation,” Greenland is arguing not that the “positive findings” of epidemiologic studies have proven the existence of a magnetic field effect, but that the objections of extreme skeptics must be made explicit: it is their presumed, if unstated, prior probability estimates that justify their conclusions about whether or not there is an actual magnetic field effect associated with childhood leukemia; it is not the data collection itself. Prior probability estimates put people’s cards on the table.

I recommend the rest of Greenland’s article, which is full of interesting stuff. For example, he doesn’t agree that “objective” Bayesian methods, using non-informative priors (see my point #7 above) are more useful than frequentist methods, since they are really doing the same thing:

…frequentist results are what one gets from the Bayesian calculation when the prior information is made negligibly small relative to the data information. In this sense, frequentist results are just extreme Bayesian results, ones in which the prior information is zero, asserting that absolutely nothing is known about the [question] outside of the study. Some promote such priors as ‘letting the data speak for themselves’. In reality, the data say nothing by themselves: The frequentist results are computed using probability models that assume complete absence of bias and so filter the data through false assumptions.

All for now. In the next post I’ll discuss another Cochrane review that has some pleasant surprises.

…

*The Prior Probability, Bayesian vs. Frequentist Inference, and EBM Series:

1. Homeopathy and Evidence-Based Medicine: Back to the Future Part V

2. Prior Probability: The Dirty Little Secret of “Evidence-Based Alternative Medicine”

3. Prior Probability: the Dirty Little Secret of “Evidence-Based Alternative Medicine”—Continued

4. Prior Probability: the Dirty Little Secret of “Evidence-Based Alternative Medicine”—Continued Again

5. Yes, Jacqueline: EBM ought to be Synonymous with SBM

6. The 2nd Yale Research Symposium on Complementary and Integrative Medicine. Part II

7. H. Pylori, Plausibility, and Greek Tragedy: the Quirky Case of Dr. John Lykoudis

8. Evidence-Based Medicine, Human Studies Ethics, and the ‘Gonzalez Regimen’: a Disappointing Editorial in the Journal of Clinical Oncology Part 1

9. Evidence-Based Medicine, Human Studies Ethics, and the ‘Gonzalez Regimen’: a Disappointing Editorial in the Journal of Clinical Oncology Part 2

10. Of SBM and EBM Redux. Part I: Does EBM Undervalue Basic Science and Overvalue RCTs?

11. Of SBM and EBM Redux. Part II: Is it a Good Idea to test Highly Implausible Health Claims?

12. Of SBM and EBM Redux. Part III: Parapsychology is the Role Model for “CAM” Research

13. Of SBM and EBM Redux. Part IV: More Cochrane and a little Bayes

14. Of SBM and EBM Redux. Part IV, Continued: More Cochrane and a little Bayes

I have a mental basket of drugs that I suspect may be placebos. In that basket were the topical versions of non-steroidal anti-inflammatory drugs (NSAIDs). When the first products were commercially marketed over a decade ago, I found the clinical evidence unconvincing, and I suspected that the modestly positive effects were probably due to simply rubbing the affected area, or possibly due to the effects of the cream or vehicle itself. Frankly, I didn’t think these products worked. So when I recently noticed a topical NSAID appear for sale as an over-the-counter treatment for muscle aches and pains (seemingly only in Canada, for now), I was confident it would make a good case study in bad science.

It’s not that I’m partial to the oral NSAIDs. Yes, they’re among the most versatile, and probably most well-loved drugs in our modern medicine cabinet. They offer good pain control, reduce inflammation and can eliminate fever. We start using it in our sick and feverish infants, through childhood and adulthood for the aches and pains of modern life, and into our later years for the treatment of degenerative disease like osteoarthritis, which affects pretty much everyone as we age. An astonishing 17 million Americans use NSAIDs on a daily basis, and this number is expected to grow as the population ages. In the running groups I frequent, ibuprofen has the affectionate nickname “Vitamin I”, where it’s perceived as an essential ingredient for dealing with the consequences of training.

But NSAIDs have a long list of side effects. Not only do they cause stomach ulcers and bleeding by damaging the gastrointestinal mucosa, there are heart risks, too. It was the arrival (and departure) of the drugs Bextra and Vioxx that led to documentation of the potential for cardiovascular toxicity. And now there’s data to suggest that these effects are not limited to the “COX-2″ drugs – almost all NSAIDs, including the old standbys we have used for years, seem capable of raising the risks of heart attacks and strokes.

So despite my initial skepticism, I took another look at the topical NSAIDs. The data were not what I expected.

The use of NSAIDs

ASA (acetylsalicylic acid, Aspirin) the prototypical NSAID, traces its origin back to willow bark, a natural source of salicylate. All NSAIDs work the same way, interrupting the production of inflammatory and pain-related hormones called prostaglandins. Since ASA’s introduction in 1897, more than two dozen chemically related drugs have come to market. They’re now among the commonly used drugs used worldwide, playing a crucial role in pain management. Given the ubiquity of acute pain conditions, as well as chronic conditions like osteoarthritis, it’s estimated that 1 in 20 physician visits are related to prescriptions for NSAIDs. In general, all NSAIDS have equivalent efficacy at the population level, though individual response, and side effects, can vary between drugs. The discovery of different forms of cyclooxygenase enzymes led to new drugs that targeted COX-2 (at sites of inflammation) rather than COX-1 (which is involved with the stomach mucosa. Inhibit COX-2 rather than COX-1, the thinking went, and you could get the antinflammatory action of a traditional NSAID without the gastrointestinal toxicity. However, as the COX-2 saga demonstrated, effects can include the creation of a significant prothrombic effect – with devastating consequences.

The Risks of NSAIDs

Prescription drugs can and do cause significant morbidity, leading to frequent hospital admissions. While we may think nothing of popping a few ibuprofen now and then, NSAIDs have been linked to about 30% of drug-related hospital admissions, and it’s estimated that 12,000-16,000 Americans die annually as a result of gastrointestinal bleeding caused by NSAIDs.

Stomach bleeding and ulcers are a consequence of an NSAID’s mechanism of action – their effect on prostaglandins. The lining of the gut is weakened, and stomach and duodenal ulcers result. Even very low doses of ASA have been documented to have measurable effects on the mucosal lining of the gastrointestinal tract. The risks of gastrointestinal toxicity are significantly increased in the elderly, in those on high doses of NSAIDs, and when combined with other drugs (e.g., steroids) that suppress normal stomach protection.

The cardiovascular risks of NSAIDs became well documented following the worldwide withdrawal of rofecoxib (Vioxx) and international examinations of the cardiovascular risks of the entire category of drugs. Data have now emerged to convincingly establish that most NSAIDs (except ASA) are associated with an increased risk of cardiovascular events. Chronic (routine) consumption of most drugs is linked to small but real increases in heart attacks and stroke. These effects may be a consequence of interference with the beneficial effects of ASA (Aspirin), direct negative cardiovascular effects, and exacerbations of fluid balance, leading to heart failure.

When it comes to cardiovascular risks, not all NSAIDs are the same. A recently published network meta-analysis summarizes the differences, and the overall risks. Both traditional NSAIDs, like naproxen, ibuprofen, and diclofenac, as well as the COX-2 selective NSAIDs, like celecoxib (Celebrex) and rofecoxib (Vioxx) were studied. Happily for those that use over-the-counter anti-inflammatories only occasionally: naproxen seems to be the safest among the NSAIDs, with little to no increase in risk, and ibuprofen’s elevated risk seems limited to regular doses of 1200mg per day or more. So for the individual consumer, when do the risks outweigh the benefits of NSAIDs? Ultimately this comes down to an individual consideration of reasons for use, risk factors, and expected benefits.

To be clear, the absolute cardiovascular risks of NSAIDs, on an individual level, are low, compared to the other side effects of NSAIDs. They seem to cause three or more excessive events like heart attacks and stroke events, per 1000 patients, per year. Compare this to the 20-40 per 1000 per year that may have a (sometimes fatal) stomach bleed, a risk that’s 4x that of non-users. Still, their risk profile suggests that a consideration of their risk and benefits is warranted, particularly when they’re being contemplated in people with preexisting cardiovascular disease. On balance, when treating short-term conditions, the incremental risk in patients without cardiovascular disease is probably very low. Still, it seems prudent to use safer alternatives first (when possible) and if using NSAIDs, considering the lowest possible dose for the shortest possible duration.

Topical NSAIDs: The evidence

Over the past two decades, evidence has emerged to demonstrate that topical versions of NSAIDs are well absorbed through the skin and reach therapeutic levels in synovial fluid; muscle, and fascia. With topical use, little drug actually circulates in the plasma, leading to levels that are a fraction of comparable oral doses. As adverse events from NSAIDs are largely dose-related, it’s expected (thought not as well documented) that serious side effects should be minimized.

For chronic conditions like osteoarthritis, the data are of fair quality and are persuasive. The National Institutes for Health and Clinical Excellence osteoarthritis guidelines provides a nice summary of the trials. Studies varied by site of osteoarthritis (knee, hand, hip, etc), the type of NSAID studied, the regimen, and trial design. On balance, there’s good evidence to show that topical NSAIDs are clinically- and cost-effective for short term (< 4 weeks) use, especially when pain is localized. Topical and oral versions seem to be similarly effective under these circumstances, and there there’s a significant reduction in non-serious adverse events with topical products. While there’s no conclusive evidence to demonstrate a reduction of serious adverse events, they’re expected to be better than oral products, given the blood levels are much lower. What impressed me is that topical NSAIDs are recommended as a preferred treatment before oral NSAIDs. And given many taking oral NSAIDs need to take stomach protecting drugs like omeprazole, the topical products, while more expensive than their oral versions, may actually be more cost-effective overall.

A Cochrane review from 2010 is equally positive about the treatment of acute pain conditions. Forty-seven trials were included in their analysis that considered topical NSAIDs for strains, sprains, and overuse-type injuries. Compared to placebo, topical NSAIDs were evaluated to be effective, with few side effects, with a number needed to treat (NNT) of 4.5. About 6 or 7 out of 10 users can expect to achieve pain control with a topical NSAID, compared to 4 with a placebo. Side effects are comparable to placebo. And given systemic absorption is lower, the serious toxicity we associate with NSAIDs should be lessened, too. Not bad.

Given there’s no long-term data with topical NSAIDs, the evidence doesn’t give us enough insight to understand the risk profile beyond a few weeks. Consequently it seems reasonable to try using topical products instead of oral products, particularly for intermittent, rather than chronic, pain conditions. While compounding pharmacies have made topical versions of NSAIDs for years, there’s little information on effectiveness and safety of these products. As commercial formulations are supported with pharmacokinetic and clinical studies demonstrating efficacy, they are the preparations of choice.

Conclusion

NSAIDs, which already had a bad side effect profile, cause more harm then we thought. Evidence has emerged to demonstrate that topical NSAIDs are effective for many conditions that might otherwise require oral therapies. There’s little evidence to demonstrate that topical NSAIDs are effective for some types of pain, like back pain, headache, or neuropathic pain. But based on what’s now known about the cardiovascular toxicity of NSAIDs, it’s likely that topical products provide a superior risk/benefit perspective for regular and occasional users. The Cochrane review points out that topical NSAIDs are widely accepted in some parts of the world, but not in others. The reasons why are not clear. But having read the evidence, I’ve changed my opinion. And when I’m recovering from my next marathon, I’ll think about reaching for a topical NSAID, instead of that comforting bottle of vitamin I.

References

Haroutiunian, S., Drennan, D., & Lipman, A. (2010). Topical NSAID Therapy for Musculoskeletal Pain Pain Medicine, 11 (4), 535-549 DOI: 10.1111/j.1526-4637.2010.00809.x

Massey T, Derry S, Moore RA, & McQuay HJ (2010). Topical NSAIDs for acute pain in adults. Cochrane database of systematic reviews (Online) (6) PMID: 20556778

Solomon DH. Up-to-Date: Nonselective NSAIDs: Overview of adverse effects; Nonselective NSAIDs: Overview of adverse effects. From Up-To-Date (Database on the Internet).

Trelle, S., Reichenbach, S., Wandel, S., Hildebrand, P., Tschannen, B., Villiger, P., Egger, M., & Juni, P. (2011). Cardiovascular safety of non-steroidal anti-inflammatory drugs: network meta-analysis BMJ, 342 (jan11 1) DOI: 10.1136/bmj.c7086

It has long been recognized that there are substantial multifactorial placebo effects that create real and illusory improvements in response to even an inactive treatment. There is a tendency, however (especially in popular discussion), to oversimplify placebo effects – to treat them as one mind-over-matter effect for all outcomes. Meanwhile researchers are elucidating the many mechanisms that go into measured placebo effects, and the differing magnitude of placebo effects for different outcomes.

For example, placebo effects for pain appear to be maximal, while placebo effects for outcomes like cancer survival appear to be minimal.

A recent study sheds additional light on the expectation placebo effect for pain. The effect is, not surprisingly, substantial. However it does not extrapolate to placebo effects for outcomes other than pain, and the results of this very study give some indication why. From the abstract:

The effect of a fixed concentration of the ?-opioid agonist remifentanil on constant heat pain was assessed under three experimental conditions using a within-subject design: with no expectation of analgesia, with expectancy of a positive analgesic effect, and with negative expectancy of analgesia (that is, expectation of hyperalgesia or exacerbation of pain).

What they found was that the positive expectation group reported twice the analgesic effect as the no expectation group, and the negative expectation group reported no analgesic effect. This is a dramatic effect, but not surprising.

There are systems in the brain that specifically alter the perception of pain. Mood, expectation, and attention all affect the perception of pain. This makes evolutionary sense, since pain is meant to be a warning system for tissue damage or disease, and so needs to have an acute grip on our attention. At the same time, there are circumstances when we may need to function despite our pain, or when it would be adaptive to habituate to chronic pain. There are therefore mechanisms in the brain that function to enhance and draw our emotional attention to pain, and others that  function to inhibit pain.

It also needs to be noted that, broadly speaking, there are two components to pain. There is the origin and transmission of the pain signal, which is perceived as any tactile sensation. But then there is a specific emotional component to pain which occurs in the brain – that processing which makes pain hurt, that makes it into an emotionally negative experience. These two components can be separated. Narcotics, for example, are especially good at blocking the emotional component of pain, so that at times patients on opiates may report that they feel the pain but it does not bother them. Additionally, while withdrawing from narcotics the emotional component of pain in enhanced – patients may have what appears to be an exaggerated emotional response to even minor pain.

Therefore – since there is a built in system for modulating pain in response to both the physical and emotional environment, it makes sense that this system can be manipulated with physical and emotional inputs. If you make a patient feel better emotionally or decrease their stress or anxiety, their perception of pain will decrease, or at least it will not bother them as much (or, more precisely, their reporting of pain will decrease). This is why multi-disciplinary pain clinics often include psychological therapy as part of the overall approach.

This study demonstrates that expectation itself can have a dramatic effect on pain perception. They further elucidate, with fMRI analysis, the neuroanatomy that underlies this effect.

These subjective effects were substantiated by significant changes in the neural activity in brain regions involved with the coding of pain intensity. The positive expectancy effects were associated with activity in the endogenous pain modulatory system, and the negative expectancy effects with activity in the hippocampus.

This finding support prior research:

Further PET studies with dopamine D2/D3 receptor-labeling radiotracer demonstrate that basal ganglia including NAC are related to placebo analgesic responses. NAC dopamine release induced by placebo analgesia is related to expectation of analgesia. These data indicate that the aforementioned brain regions and neurotransmitters such as endogenous opioid and dopamine systems contribute to placebo analgesia.

The fMRI shows us where the effect is, and the PET scanning additionally shows us that dopamine is the important neurotransmitter involved in this effect.

What I would have loved to have seen in this study (perhaps this will be part of a follow up) is the same three treatment arms with a placebo treatment. This would enable us to directly compare the relative size of the expectation effect to the opiate effect. There are other questions as well. How much variation is there in the magnitude of this effect from person to person? Does the expectation effect habituate over time? Is the magnitude the same for different kinds of pain?

Conclusion

This study reinforces prior research indicating that there are built-in neurological mechanisms that modulate the perception and emotional content of pain. The study gives us further information about the exact brain structures involved in this effect. The authors conclude:

We propose that it may be necessary to integrate patients’ beliefs and expectations into drug treatment regimes alongside traditional considerations in order to optimize treatment outcomes.

They should have added “for pain.” This study says nothing about other treatment effects for which there does not exist a target system for symptom modulation. This error is distressingly common, especially in the translation of such research to the public. Pain is uniquely amenable to manipulation through mood and expectation. This does not predict that any other symptom or disease state can be so manipulated.

This situation is analogous to stress and heart disease. The heart is specifically susceptible to the physiological effects of emotional stress. Stress reduction, therefore, decreases, for example, the risk of heart attack. This does not mean, however, that stress reduction will therefore decrease the risks of any disease or adverse outcome.

All too often, however, people speak of “the placebo effect” as if it is one effect, equal for all outcomes. This notion is then supported with hand-waving explanations about self-healing. But the research is actually quite clear. There are many placebo effects. Expectation is only one effect among many,  and many of these effects are illusory – they create the false appearance of improvement where none exists (like regression to the mean or observational bias). Further, when speaking of the expectation effect we must be careful not to falsely extrapolate this effect from one outcome (like pain) to others.

This and other studies show that the brain is hardwired to modulate pain based upon expectation. There is no reason to think that this effect translates to other subjective symptoms, let alone objective outcomes like survival.

But I do agree with the authors to the extent that this and other studies do suggest that practitioners should seek to ethically maximize the benefits of positive expectation when treating pain. This should not, of course, violate the principles of honesty or informed consent. But putting a positive spin on the potential of a pain intervention is therapeutic. This does not justify, in my opinion, using a known placebo intervention (unless the patient was informed that it was a placebo or a treatment without any biological activity), because otherwise this would involve unethical deception (and could also create and reinforce unscientific beliefs in patients that could result in harm downstream). Further, as this study shows, you can get a sizable placebo effect from physiologically effective treatments.

A new article in the Journal of Women’s Health by Westhoff, Jones, and Guiahi asks “Do New Guidelines and Technology Make the Routine Pelvic Examination Obsolete?”

The pelvic exam consists of two main components: the insertion of a speculum to visualize the cervix and the bimanual exam where the practitioner inserts two fingers into the vagina and puts the other hand on the abdomen to palpate the uterus and ovaries. The rationales for a pelvic exam in asymptomatic women boil down to these:

• Screening for Chlamydia and gonorrhea
• Evaluation before prescribing hormonal contraceptives
• Screening for cervical cancer
• Early detection of ovarian cancer

None of these are supported by the evidence. Eliminating bimanual exams and limiting speculum exams in asymptomatic patients would reduce costs without reducing health benefits, allowing for better use of resources for services of proven benefit. Pelvic exams are necessary only for symptomatic patients and for follow-up of known abnormalities.

Screening for Chlamydia and Gonorrhea

Screening for Chlamydia in young women is evidence-based: it reduces the rate of pelvic inflammatory disease. New tests are available (on urine and self-administered vaginal swabs) that do not require a pelvic exam by a doctor. They are sensitive and cost-effective. Supporting references are listed in the article.

Hormonal Contraception

Doctors used to require pelvic exams before they would dispense prescriptions for oral contraceptives. This was never shown to be necessary; no findings from these exams influenced the decision to issue a prescription. One concern, the possibility of a pre-existing pregnancy, can’t be entirely ruled out by a pelvic exam; but the risk can be minimized by starting the pills after a normal menstrual period. Now all the major guidelines (from the FDA, WHO, ACOG, Planned Parenthood, etc.), specify that a pelvic exam is not required for hormonal contraception.

Cervical Cancer Screening

Pap smears have been proven effective in reducing morbidity and mortality from cervical cancer. Speculum exams are necessary to obtain specimens for Pap smears, but Pap smears need not be done annually and speculum exams need not be accompanied by bimanual exams. Current recommendations are to begin screening at age 21 and to re-screen at intervals of 2-3 years. New technology currently in development may eventually allow for equivalent screening without a pelvic exam.

Ovarian Cancer

The evidence shows that bimanual exams are useless for detecting ovarian cancer, and they are no longer recommended for this purpose.

Other Benefits/Risks of Pelvic Exams

While other conditions such as fibroids, ovarian cysts, and yeast infections can be detected by examining asymptomatic women, there is no evidence that early diagnosis improves outcomes. Over-screening for cervical cancer has been shown to lead to harm. Findings on pelvic exams can be false positives and can lead to unnecessary interventions.

“U.S. rates of ovarian cystectomy and hysterectomy are more than twice as high as rates in European countries, where the use of the pelvic examination is limited to symptomatic women.”

Is It Time to Abandon the Annual Pelvic Exam?

Yes, I think so. The existing evidence indicates that omitting it in asymptomatic women would not affect health outcomes. This article is representative of a growing consensus in the medical community, especially in other countries; but many US doctors are still doing annual pelvic exams. I suspect (just my opinion) that they are afraid of looking stupid or getting sued if they miss something, or are clinging to what they were taught to do out of inertia.  Meanwhile, science-based doctors are leaning away from annual physical exams in general. As this website says,

The annual physical exam is beloved by many people and their doctors. But studies show that the actual exam isn’t very helpful in discovering problems. Leading doctors and medical groups have called the annual physical exam “not necessary” in generally healthy people.

Even in patients being followed for diagnosed diseases, the physical exam sometimes degenerates into a token ritual. I’ve noticed that although I have no heart or lung symptoms, my own doctors like to check my lungs at every visit by putting the stethoscope on four spots (right, left, front and back) for one breath each, and to check my heart by applying the stethoscope briefly to one spot. I tolerate it because I know it makes them feel better, but I consider it totally useless.
Admittedly, there is a human element involved: hands-on interactions and the perception of “doing something” can be reassuring and can enhance the doctor/patient relationship. But can’t a caring clinician attain those same benefits within the realm of science-based medicine? A doctor’s time is better spent on proven health screening measures and in educating and counseling patients than in carrying out nonproductive rituals.

Now here’s something that can be used to counter the antivaccine musical stylings of Mike Adams and his song Don’t Inject Me: Play ZDoggMD’s Immunize!:

Sometimes, even on SBM, we need to lighten things up a bit. Take that, Mike Adams!

Last Friday, Mark Crislip posted an excellent deconstruction of a very disappointing article that appeared in the most recent issue of Skeptical Inquirer, the flagship publication of the Committee for Skeptical Inquiry (CSI). I say “disappointing,” because I was disappointed to see SI (Skeptical Inquirer, not Sports Illustrated) publish such a biased, poorly thought out article, apparently for the sake of controversy. I’m a subscriber myself, and in general enjoy reading the magazine, although of late I must admit that I don’t always read each issue cover to cover the way I used to do. Between work, grant writing, blogging, and other activities, my outside reading, even of publications I like, has declined. Perhaps SI will soon find itself off my reading list. Be that as it may, I couldn’t miss the article that so irritated Mark, because it irritated me as well. There it was, emblazoned prominently on the cover of the March/April 2011 issue: Seven Deadly Medical Hypotheses. I flipped through the issue to the article to find out that this little gem was written by someone named Reynold Spector, MD. A tinge of familiarity going through my brain, I tried to think where I had heard that name before.

And then I remembered.

Dr. Spector, it turns out, first got on my nerves about a year ago, when he wrote an article for the January/February 2010 issue of SI entitled The War on Cancer A Progress Report for Skeptics. I remember at that time being irritated by the article and wanting to pen a discussion of the points raised but don’t recall why I never actually did. It was probably a combination of the fact that SI doesn’t publish its articles online until some months have passed after the paper version has been released and perhaps my laziness about having to manually transcribe with my own fingers any passages of text that I might want to cite. By the time the article was available online, I forgot about it and never came back to it–until now. I should therefore, right here, right now, publicly thank Mark (and, of course, Dr. Spector) for providing me the opportunity to revisit that article in the context of piling on, so to speak, Dr. Spector’s most recent article. After all, Deadly Hypothesis Seven (as Dr. Spector so cheesily put it) is:

From a cancer patient population and public health perspective, cancer chemotherapy (chemo) has been a major medical advance.

Dr. Spector then takes this opportunity to cite copiously from his 2010 article, sprinkling “(Spector, 2010)” throughout the text like powdered sugar on a cupcake. There’s the opening I needed to justify revisiting an article that’s more than a year old! And what fantastic timing, too, hot on the heals of my post from a couple of weeks ago entitled Why haven’t we cured cancer yet?

Back to the future, before visiting the past

Before I leap back more than a year, first let me just point out that I agree with Mark 100% when he castigated Dr. Spector for his opening volley. Although thought had never occurred to me at the time, in retrospect I even agree with Crislip’s likening Dr. Spector’s tirade to a Mike Adams screed, at least in dogmatic certainty and tone. Sadly, for entertainment value at least, Dr. Spector lacks the looney hyperbole of Mike Adams. Also, unlike Adams, Dr. Spector is a real scientist, but damn if, references omitted, this first sentence couldn’t have come right out of a Mike Adams special:

A chronic scandal plagues the medical and nutritional literature (Spector and Vessell, 2006; Spector, 2009): much of what is published is erroneous, pseudoscientific, or worse.

Like Mark, I’m a John Ioannidis convert, and I accept that there is a lot of medical literature that is erroneous. (Just search for Dr. Ioannidis’ last name on this blog, and you’ll find copious posts praising him and discussing his work.) In fact, as I’ve pointed out, most medical researchers instinctively know that most new scientific findings will not hold up to scrutiny, which is why we rarely accept the results of a single study, except in unusual circumstances, as being enough to change practice. I also have pointed out many times that this is not necessarily a bad thing. Replication is key to verification of scientific findings, and more often than not provocative scientific findings are not replicated. Does that mean they shouldn’t be published?

As for pseudoscience, I’m half tempted to agree with Dr. Spector, but just not in the way he thinks. Unfortunately, over the last 20 years or so, there has been an increasing amount of pseudoscience in the medical literature in the form of “complementary and alternative medicine” (CAM) studies of highly improbable remedies or even virtually impossible ones (i.e., homeopathy). However, that does not appear to be what Dr. Spector is talking about, which is why I looked up his references. The second reference is to an SI article from 2009 entitled Science and Pseudoscience in Adult Nutrition Research and Practice. There, and only there, did I find out just what it is that Dr. Spector apparently means by “pseudoscience”:

By pseudoscience, I mean the use of inappropriate methods that frequently yield wrong or misleading answers for the type of question asked. In nutrition research, such methods also often misuse statistical evaluations.

Ah, now I get it! Dr. Spector doesn’t really know the difference between inadequately rigorous science and pseudoscience! Now, don’t get me wrong. I know that it’s not always easy to distinguish science from pseudoscience, especially at the fringes, but in general bad science has to go a lot further than Dr. Spector thinks to merit the the term “pseudoscience.” It is clear (to me, at least) from his articles that Dr. Spector throws around the term “pseudoscience” around rather more loosely than he should, using it as a pejorative for any clinical science less rigorous than a randomized, double-blind, placebo-controlled trial that meets FDA standards for approval of a drug (his pharma background coming to the fore, no doubt). Pseudoscience, Dr. Spector. You keep using that word. I do not think it means what you think it means. Indeed, I almost get the impression from his articles that Dr. Spector views any study that doesn’t reach FDA-level standards for drug approval to be pseudoscience. He also piles on nutritional science (that is, after all, his area of specialty), and there is no doubt that here is a lot of pseudoscience there; however the vast majority of it is not in the scientific literature. Rather, it’s snake oil salesmen selling diets and supplements based on less rigorous science, the willful twisting and misinterpretation of acceptable science, and making up claims out of whole cloth.

Here’s the deal. Medical science, when it works well, tends to progress from basic science, to small pilot studies, to larger randomized studies, and then–only then–to those big, rigorous, insanely expensive randomized, double-blind, placebo-controlled trials. Dr. Spector mentions hierarchies of evidence, but he seems to fall into a false dichotomy, namely that if it’s not Level I evidence, it’s crap. The problem is, as Mark pointed out, in medicine we often don’t have Level I evidence for many questions. Indeed, for some questions, we will never have Level I evidence. Clinical medicine involves making decisions in the midst of uncertainty, sometimes extreme uncertainty. One example is hormone replacement therapy for menopause before the results of the Women’s Health Initiative study were reported. Indeed, Dr. Spector makes much hay out of the widespread use of hormone replacement therapy (HRT) back in the 1980s and 1990s, as an example of what happens when we don’t adhere to proper clinical trial design, labeling Deadly Hypothesis Two as:

The hypothesis was that if women replace these hormones postmenopausally with HRT, they will remain “youthful” and not suffer from heart disease, dementia, vaginal dryness, hot flashes, and fractured bones.

Dr. Spector then proceeds to paint a picture of reckless physicians proceeding on crappy studies to pump women full of hormones. Actually, it was more than a bit more complicated on than that. That was the time when I was in my medical training, and I remember the discussions we had regarding the strength (or lack thereof) of the epidemiological data and the lack of good RCTs looking at HRT. I also remember that nothing works as well to relieve menopausal symptoms as HRT, an observation we have been reminded of again since 2003, which is the year when the first big study came out implicating HRT in increasing the risk of breast cancer (more later). It’s also hard not to point out that, these days, it’s not physicians promoting HRT. Rather, it’s women like Suzanne Somers promoting “bioidentical hormones” and telling postmenopausal women that they should strive for the estrogen levels that they had when they were 25. Be that as it may, I found a rather fascinating editorial in the New England Journal of Medicine from more than 20 years ago that discussed the state of the evidence back then with regard to estrogen and breast cancer:

Evidence that estrogen increases the risk of breast cancer has been surprisingly difficult to obtain. Clinical and epidemiologic studies and studies in animals strongly suggest that endogenous estrogen plays a part in causing breast cancer. If so, exogenous estrogen should be a potent promoter of breast cancer. Although more than 20 case–control and prospective studies of the relation of breast cancer and noncontraceptive estrogen use have failed to demonstrate the expected association, relatively few women in these studies used estrogen for extended periods. Studies of the use of diethylstilbestrol and oral contraceptives suggest that a long exposure or latency may be necessary to show any association between hormone use and breast cancer. In the Swedish study, only six years of follow-up was needed to demonstrate an increased risk of breast cancer with the postmenopausal use of estradiol. It should be noted, however, that half the women in the subgroup that provided detailed data on the duration of hormone use had taken estrogen for many years before their base-line prescription status was defined. The duration of estrogen exposure in these women before the diagnosis of breast cancer was probably seriously underestimated; a short latency cannot be attributed to estradiol on the basis of these data. Other recent studies of the use of noncontraceptive estrogen suggest a slightly increased risk of breast cancer after 15 to 20 years’ use.

One notes that, even now, the evidence is conflicting regarding HRT and breast cancer, with the preponderance of evidence suggesting that mixed HRT (estrogen and progestin) significantly increases the risk of breast cancer, while estrogen-alone HRT very well might not increase the risk of breast cancer at all or (more likely) only very little. Indeed, I was just at a conference all day Saturday where data demonstrating this very point were discussed by one of the speakers. None of this stops Dr. Spector from categorically labeling estrogen as a “carcinogen that causes breast cancers that kill women.” Maybe. Maybe not. It’s actually not that clear. The problem, of course, is that, consistent with the first primary reports of WHI results, the preponderance of evidence finding health risks due to HRT have indicted the combined progestin/estrogen combinations as unsafe. Even at this late time, we do not truly know whether estrogen-alone HRT carries significant risks (there are even some studies, a subgroup of the WHI included, that hint at a slightly protective effect of estrogen against breast cancer), but we do have a pretty good idea that estrogen-alone HRT is almost certainly safer than estrogen-progestin HRT, at least with respect to breast cancer. Unfortunately, there is good evidence that estrogen-only HRT increases the risk of uterine cancer. Either way, Dr. Spector’s dogmatic and unnuanced discussion of the issue suggests an axe to grind more than an interest in providing an accurate picture. Indeed, he even goes so far as to slip this sentence in there: “In legal challenges the U.S. Supreme Court has upheld the notion that HRT causes breast cancer.”

What? Who cares what the Supreme Court says about medical causation? That’s a legal standard, not a scientific standard! There’s no reason to throw such a sentence into a serious medical article.

The rest of the “Seven Deadly Medical Hypotheses” remain just as questionable, particularly the way Dr. Spector castigates the idea that screening populations for breast and prostate cancer saves lives. In all fairness, Dr. Spector’s skepticism towards screening is actually the least unreasonable part of his most recent article, given recent evidence. He even concludes that mammography has a small benefit. Therein lies a contradiction. If mammography, for instance, is beneficial, even if only slightly, then how can it be part of a “deadly medical hypothesis”? Calling screening a “deadly” medical hypothesis is, as is the case with much of this article, way over the top. A “disappointing” medical hypothesis would be a far better description. In any case, for a far more nuanced discussion of cancer screening, I will blow my own horn and suggest that you go to read these posts:

Posts by yours truly:

1. The early detection of cancer and improved survival: More complicated than most people think
2. Early detection of cancer, part 2: Breast cancer and MRI
3. Do over one in five breast cancers detected by mammography alone really spontaneously regress?
4. Are one in three breast cancers really overdiagnosed and overtreated?
5. The cancer screening kerfuffle erupts again: “Rethinking” screening for breast and prostate cancer
6. The USPSTF recommendations for breast cancer screening: Not the final word
7. The mammography wars heat up again
8. Molecular breast imaging (MBI): A promising technology oversold in a TED Talk?

Posts by Harriet Hall:

1. Screening Tests – Cumulative Incidence of False Positives
2. Overdiagnosis

By Val Jones:

• The Mammogram Post-Mortem

Read them now, or read them later. They are far more informative and nuanced than anything Dr. Spector has written on these topics for SI. For example, you won’t find the word “deadly” in there anywhere. In the meantime, let’s move on to the article that irritated me so over a year ago. Oddly enough, it was a bit more balanced and less dogmatic than the current article.

“We’re losing the war on cancer”?

The beginning of The War on Cancer A Progress Report for Skeptics, while not as over-the-top as the beginning of Seven Deadly Medical Hypotheses, is still pretty negative:

In 1971, President Nixon and Congress declared war on cancer. Since then, the federal government has spent well over $105 billion on the effort (Kolata 2009b). What have we gained from that huge investment? David Nathan, a well-known professor and administrator, maintains in his book The Cancer Treatment Revolution (2007) that we have made substantial progress. However, he greatly overestimates the potential of the newer so-called “smart drugs.” Re searchers Psyrri and De Vita (2008) also claim important progress. However, they cherry-pick the cancers with which there has been some progress and do not discuss the failures. Moreover, they only discuss the last decade rather than a more balanced view of 1950 or 1975 to the present.

On the other hand, Gina Kolata pointed out in The New York Times that the cancer death rate, adjusted for the size and age of the population, has decreased by only 5 percent since 1950 (Kolata 2009a). She argues that there has been very little overall progress in the war on cancer.

I find it rather amusing how Dr. Spector accuses investigators like Dr. Vincent DeVita (who is a coauthor of one of the widely used textbooks of oncology there is, a copy of which sits on my shelf in my office) of “cherry picking” cancers for for which progress has been made and focusing primarily on the last decade while at the same time stating that he is going to focus on adult solid cancers, where less progress has been made. One might argue that this is a correct way to do it, and far be it from me to claim that the war on cancer has been an overwhelming success. As I pointed out a couple of weeks ago, however, there is a reason (many reasons, actually) why progress has been so elusive. There is also at least one other reason. However, it’s quite obvious in both articles that Dr. Spector has himself concentrated on data that he can use to make the situation look as dismal as possible; i.e., to support his apparently preconceived conclusions that the war on cancer has been a miserable failure and that chemotherapy doesn’t work (that is, except when it does work very well). Indeed, in his most recent article, Dr. Spector uses terminology that is even more negative about chemotherapy than in his previous article. For example in the current article, Dr. Spector writes:

The hypothesis behind current chemotherapy is deeply flawed. How can we expect these drugs, most of which are nonspecific cellular poisons, to kill only wiley cancer cells and not normal cells? In fact, cacner chemotherapy routinely kills bone marro and the cell lining of the gastrointestinal tract, with very distressing (indeed sometimes fatal) side effects.

It rather shocks me that a pharmacologist like Dr. Spector would write something like this without mentioning that the reason chemotherapy can work in some tumors is because it is more toxic to the cancer cell than it is to (most of) the surrounding normal tissue. The same thing is true of radiation. This is not a trivial point. Dr. Spector makes it sound as though chemotherapy poisons everything equally and that it’s a miracle that it ever works at all. He then writes:

However, it cannot be denied that there are a few populations for which chemotherapy is marvelously effective, as noted above, and must be used.

No kidding! For example, many leukemias and lymphomas, testicular cancer, and anal cancer (which is treated primarily with the Nigro protocol, which consists of chemotherapy and radiation), among others!

Dr. Spector correctly points out that smoking tobacco products is a major cause of lung cancer, which causes most cancer deaths these days in both men and women. He even shows several very nice graphs that demonstrate that lung cancer death rates began to skyrocket about twenty years after cigarette consumption began to skyrocket (Figure 3) and that lung cancer death rates have been declining (in men at least; they appear to be peaking in women, Figures 4 and 5), approximately 25 years after cigarette consumption began to decline. All of these results are very much in accord with what we know about cigarette smoke as a carcinogen. One thing is clear: If we could eliminate cigarette smoking completely, approximately 20 years later, declines in lung cancer deaths would drive major declines in overall cancer deaths. There’s little doubt of that. However, such an observation is very much a “Well, duh!” conclusion. It’s not as though public health authorities in the U.S are unaware of such statistics or that dramatic gains or haven’t been working to try to discourage smoking. Changing behavior is very, very hard. In fact, I would argue that decreasing cancer mortality by 5% since 1950 is actually pretty darned good, given that lung cancer mortality tripled among men between 1950 and 1990 and more than doubled among women from 1970 to 2000. If you don’t believe me, take a look at these graphs from the SEER Database of cancer death rates from the various major forms of cancer, in particular Figure 4 and Figure 5. Then there is this graph in Figure 2:

This demonstrates that, although cancer incidence rates are leveling off, cancer death rates are decreasing. Sure, it’s not as good as we need to do, but notice that the curves are separating. Indeed, if you look at Figure 7, you’ll see an estimate of how high cancer mortality would be if cancer mortality rates had remained the same over the last 20 years:

The American Cancer Society attributes the decreases in cancer mortality to this:

The decrease in lung cancer death rates among men is due to a reduction in tobacco use over the past 50 years, whereas the decrease in death rates for female breast, colorectal, and prostate cancer largely reflects improvements in early detection and/or treatment. Between 1990–1991 and 2006, death rates increased for liver cancer in both men and women, esophageal cancer and melanoma in men, and lung and pancreatic cancer in women. Figure 7 shows the total number of cancer deaths avoided since death rates began to decrease in 1991 in men and in 1992 in women. Approximately 767,000 cancer deaths (561,400 in men and 205,700 in women) were averted between 1991–1992 and 2006.

Death rates from all cancer are a rather crude measure of how the war on cancer is going, anyway, being an aggregate number that is only likely to be affected very late as a result of improvements in cancer therapy. Our population is aging, which means that more people are living long enough to develop cancer, particularly given that we’ve made such dramatic progress in decreasing death rates from cardiovascular disease. People who live longer because they don’t die of cardiovascular disease have to die of something, and cancer, being number two (although not for long), is the next most likely cause. In any case, let me provide an example of what I find wrong with Dr. Spector’s thesis. In his “war on cancer” article a year ago, Dr. Spector wrote:

The FDA has approved bevacizumab for the cancers listed in table 5 (Physicians Desk Reference [PDR] 2009; Health Agencies Update 2009). Since the median survival of colorectal cancer is eighteen months, bevacizumab therapy would cost about $144,000 (in such a patient) for four months prolongation of survival (Keim 2008). In the other cancers in table 4, there is no prolongation of survival. Moreover, bevacizumab can have terrible side effects, including gastrointestinal perforations, serious bleeding, severe hypertension, clot formation, and delayed wound healing (PDR 2009). By the criteria in table 4, bevacizumab is at best a marginal drug. It only slightly prolongs life, demonstrable only in colorectal cancer, has serious side effects, and is very expensive.

Here’s a more provocative and somewhat more optimistic assessment of the progress we’ve made in treating metastatic colorectal cancer in graph form (click to make bigger):

Untreated metastatic colorectal cancer has about a four to six month median survival. Our old chemotherapy regimens increased the medical survival in metastatic colorectal cancer to around 12 months. Newer regimens boosted that to around 16 or 17 months. Adding bevacizumab then increased the survival to around 21 months. All of this has occurred since the mid-1990s. Is it enough? Of course not! But as a clinician I would argue that quadrupling the life expectance of someone with metastatic colorectal cancer is nothing to sneeze at. Indeed, I even have personal experience with this. The father of a good friend died last summer of metastatic colorectal cancer after having lasted over six years. A combination of surgeries, chemotherapy, and other treatments kept him going. He played golf until a week before his health declined precipitously and unexpectedly, and he died. Yes, he was certainly an outlier, but if the median survival of a group of cancer patients is pushed longer and longer, there will be more and more outliers like my friend’s father. True, we would much prefer a cure (or at least a reasonable chance of a cure), but ask the cancer patient what that extra year or several months means to him or her. Also true, as a society, we have to decide how much we are willing to pay for that additional survival, but that is a societal question more than anyone else. It’s also rather disappointing that Dr. Spector would describe bevacizumab as a “nonspecific toxin” that interferes with blood vessel growth throughout the body. That’s not quite true. Bevacizumab does interfere with angiogenesis, but it tends to be much more specific for tumor blood vessels and other abnormal blood vessels than for normal blood vessels. Indeed, the most recent concepts regarding bevacizumab is that it actually “normalizes” tumor blood vessels, allowing chemotherapy to get to the tumor better. This observation explains a paradoxical observation that I made in the 1990s that radiation and antiangiogenic therapy with anti-VEGF antibody produced greater than additive anti-tumor effects.

Be that as it may, suppose I’ll be accused of “cherry picking” this example, but I don’t care that much. I choose it because I want to point out that the situation is not always as grim as Dr. Spector claims and that we have made enormous progress in treating some cancers over the last 40 years. I would also point out that the $105 billion we have spent on the war on cancer since 1970 breaks down to only around $2.6 billion a year. In recent years, the yearly budget for the National Cancer Institute has hovered in the $4.7 to $5.2 billion range. This may sound like a lot of money, but in reality it is only 0.1% of the $3.8 trillion federal budget this year. Let’s just put it this way, the entire yearly budget for the NCI would fund the war in Afghanistan for approximately 16 or 17 days. That is not a lot of money in the grand scheme of things; certainly it isn’t enough money to pay for a real “war” on cancer.

Where do we go from here?

Let me just begin my conclusion by conceding that Dr. Spector does make a few good points, albeit in insufficient detail in some cases. For example, his discussion of lead time bias is superficial and doesn’t even use the proper term for the concept, and he leaves out the concept of length bias in screening altogether. More irritating, though, is that there’s clearly a relentless effort on his part in both articles to paint as grim a view of the situation as before. Yes, Dr. Spector is correct that, if we could only decrease smoking to nothing we could decrease the death rate from breast cancer dramatically over the next 20-30 years. He’s also correct that decreasing use of HRT will help decrease the death rate from breast cancer, but in reality we’ve already done that. HRT use has declined precipitously after 2002; there isn’t much room to decrease it further. He also recommends vaccines to prevent HPV infection and thereby decrease the risk of cervical cancer, but that is really a pretty small contribution to the overall cancer death rate. Even so, let’s say we do all these things that Dr. Spector suggests because they are good things to do and will have an effect. Ignore for the moment how difficult it is to get people to stop smoking to prevent lung cancer, to stop drinking to prevent head and neck, esophageal, and liver cancers, and to lose weight to decrease the incidence of obesity-related cancers. Let’s say we can do it. What then? We will still have lots of people who will develop cancer and die from it if we don’t come up with better therapies. How do we do that? On that score, Dr. Spector is profoundly self-contradictory. I’ll show you what I mean.

At one point, Dr. Spector opines:

In my view the principal problem is that we just do not understand the causes of most cancers. We don’t even know if the problem is genetic or epigenetic or something totally unknown. In theory, problems 2 through 6 in table 6 are all correctable with political and scientific will and more knowledge. Even though we know cancer of the lung is caused by cigarette smoking, we do not know the mechanism, and (except for surgery) we do not know how to meaningfully intervene (see table 2). The pharmaceutical industry cannot make real progress until we understand the mechanisms and molecular causes of cancer so that industrial, academic, and governmental scientists have rational targets for intervention. We will make no progress if there are five hundred or more genetic abnormalities in a single cancer cell. Where would one begin?

And:

Moreover, with better mechanistic understanding of cancer, we could make truly “smart” drugs, as has been done in recent years for atherosclerosis (heart attacks), hypertension (strokes), gastrointestinal diseases (ulcers), and AIDS—with truly remarkable results. Let us hope cancer is next.

I can’t argue with that. Indeed, I’m very much about trying to understand the biology of cancer much better, so that we can design treatments that will be much more effective, “truly smart drugs,” as Dr. Spector puts it. That’s the direction, in fact, that I’m trying to move my research effort, with the help of a very good systems biologist. Here’s the problem. In his most recent article, Dr. Spector dismisses as useless and deadly the very techniques that we will require in order to generate the hypotheses that could lead to that better understanding of cancer upon which Dr. Spector’s proposed next generation of “smart drugs” would be based. Yet Dr. Spector poo-poos genome-wide association studies (GWAS), using them as an example of Deadly Hypothesis One. He lambastes the concept of personalized medicine and the genetic studies that will be necessary to achieve it as Deadly Hypothesis Six. He praises the methods used by the FDA, but, as explained by Mark Crislip, the rigor demanded by the FDA is the final step in a long process that begins with basic science, progresses through epidemiology and pilot studies, and then finally concludes with large, phase III randomized trials. Moreover, the final studies leading to FDA approval really are the “safest” part of the process, based on scads of data from all those earlier studies.

In other words, Dr. Spector, while claiming we need new and innovative hypotheses and ways to understand biology is in reality advocating very safe science indeed.

Dr. Spector makes a point that we need a better understanding of cancer, but he clearly has little idea about how to bring that about from a basic science perspective. So boxed into his clinical trial and pharma perspective is he that he castigates the very means of developing new hypotheses to test that we need. While Dr. Spector is correct that GWAS and gene expression profiling studies have been disappointing thus far, one needs to remember that the technology to do these studies has been in existence only a relatively few years and that these studies generate huge masses of data that strain even the best computers to analyze. In other words, we are early into these processes, but, as the cancer genome anatomy project demonstrates, we are learning.

That’s why I conclude that the worst aspect of Dr. Spector’s most recent article and his whole attitude in general is how he labels as Deadly Hypothesis One the concept that either “the investigator does not need a specific hypothesis and/or can use an inadequate method to test the hypothesis.” Yes, failing to use a specific hypothesis is not a good idea later in the process of drug development, but if we are to understand the biology of cancer sufficiently to design the next generation of “smart drugs,” we need new hypotheses, and these come from pilot studies. We sometimes call these studies “fishing expeditions” or, less pejoratively, “hypothesis generating experiments.” Come to think of it, one wonders whether Dr. Spector approved of the Human Genome Project. After all, there was no hypothesis to test there; scientists were simply trying sequence the entire human genome, and they learned a lot. More importantly, the results of the HGP generated many new hypotheses to test, many of which are being tested now, along with a revolution in genomic technology. The problem with Dr. Spector’s point of view is that he strikes me as seeing everything through the lens of pharma and the FDA. Scientific rigor is a good thing before approving drugs and treatments; in fact, it’s absolutely essential. However, the discovery process often begins by looking around and seeing if there’s anything interesting to see. Without that discovery process, all those rigorous trials meeting FDA requirements would never come to fruition because there would be no basic science pipeline to supply the translational research pipeline that eventually results in new drugs. Many–the vast majority, actually–of these hypotheses will never pan out, but they are just as essential to science-based medicine as the studies Dr. Spector loves.

Can we do better in the “war on cancer”? Of course we can–and must. However, it must be remembered that the “war on cancer,” like most wars, is not World War II. There is not, nor will there be, a total victory, an atomic bomb-like magic bullet that destroys all cancer. There will, as with most wars, be equivocal results, wins and losses, and pyrrhic victories. But we won’t get even that far if we embrace scientific nihilism over healthy skepticism.