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Health news:
 
June 2010 - Dec 2013

Minimizing breast cancer risk

May 2010

Time to move beyond salt ?

Salt hypothesis vs. reality

Is sodium bad?

April 2010

Salt studies: the latest score

From Dahl to INTERSALT

Salt hypothesis' story

March 2010

Salt war

Do bone drugs work?

Diabetes vs. drugs, 3:0

February 2010

The MMR vaccine war: Wakefield vs. ?

Wakefield proceedings: an exception?

Who's afraid of a littl' 1998 study?
 

January 2010

Antibiotic children

Physical activity benefits late-life health

Healthier life for New Year's resolution

 

December 2009

Autism epidemic worsening: CDC report

Rosuvastatin indication broadened

High-protein diet effects

 

November 2009

Folic acid cancer risk

Folic acid studies: message in a bottle?

Sweet, short life on a sugary diet

 

October 2009

Smoking health hazards: no dose-response

C. difficile warning

Asthma risk and waist size in women

 

September 2009

Antioxidants' melanoma risk: 4-fold or none?

Murky waters of vitamin D status

Is vitamin D deficiency hurting you?

 

August 2009

Pill-crushing children

New gut test for children and adults

Unhealthy habits - whistling past the graveyard?

 

July 2009

Asthma solution - between two opposites that don't attract

Light wave therapy - how does it actually work?

Hodgkin's lymphoma in children: better alternatives

 

June 2009

Hodgkin's, kids, and the abuse of power

Efficacy and safety of the conventional treatment for Hodgkin's:
behind the hype

Long-term mortality and morbidity after conventional treatments for pediatric Hodgkin's

 

May 2009

Late health effects of the toxicity of the conventional treatment for Hodgkin's

Daniel's true 5-year chances with the conventional treatment for Hodgkin's

Daniel Hauser Hodgkin's case: child protection or medical oppression?

April 2009

Protection from EMF: you're on your own

EMF pollution battle: same old...

EMF health threat and the politics of status quo
 

March 2009

Electromagnetic danger? No such thing, in our view...

EMF safety standards: are they safe?

Power-frequency field exposure
 

February 2009

Electricity and health

Electromagnetic spectrum: health connection

Is power pollution making you sick?

January 2009

Pneumococcal vaccine for adults useless?

DHA in brain development study - why not boys?

HRT shrinks brains

NEWS ARCHIVE
2009
2008
2007

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June 2010 - December 2013

II - Mammography

9. Mammography benefits:
Breast cancer mortality reduction

2 good choices to prevent breast cancer

I - BREAST CANCER
 RISK FACTORS
  

II - SCREENING X-RAY MAMMOGRAPHY

III - ALTERNATIVE TESTS

The biggest risk factor
Risk factors overview
Times change

END OF A MYTH
The whistle
Contra-argument
Last decade
Current picture

 OTHER  X-RAY TESTS
Digital standard
Tomosynthesis
Breast CT

Predisposing factors
Diet       Other

BENEFIT
Earlier diagnosis
Fewer breast cancer deaths

Gamma-ray tests
BSGI/MBI 
PEM

INITIATING  FACTORS
Radiation
Chemicals
Viruses

RISK  &  HARM

OTHER  TESTS
Breast MRI
Ultrasound
Thermography
AMAS test

INACCURACY RISKS

False negative
False positive
Overdiagnosis
PROMOTING  FACTORS
Hormonal

Non-hormonal

RADIATION

Radiation primer
Screen exposure
Radiation risk
PHYSICAL EXAM
Clinical
Self-exam

Higher all-cause mortality?

• Minimizing breast cancer risk

The most important benefits of screening healthy women, advertised officially for decades, were less invasive treatments due to earlier detection, better chance for recovery and, directly related to it, reduction in breast cancer mortality (BCM). Higher detection sensitivity, as shown on the previous page, turned into a negative: screened population consistently scores more diagnoses - due to diagnosing pseudo-cancers as real - and undergoes more treatment.

As for the better chance for recovery, it should have its final proof in the significantly reduced BCM rate. Does it?

Typically, BCM reduction figure used in promoting screening of healthy women was taken from those trials that have come up with the largest mortality reduction. Seems as if no one wanted to pay attention to the obvious contradiction. Those very trials had:

the longest interval between screening (Two-County trial),

had no more than 2-3 screenings for the majority of women (Two-County and Stockholm trials),

started systematic screening of the women in the control group in as little as 3-5 years after beginning (Two-County, Göteborg, Stockholm), or

had lower-quality mammography equipment (New York, where only 15% of breast cancers in the screened group was detected by mammography alone, which also did not detect a single cancer smaller than 1cm).

More importantly, a closer scrutiny of how large screening mammography trials were designed and executed revealed that those reporting significant BC mortality reduction benefit had serious quality issues - so much so that their results cannot be considered reliable.

Following table summarizes quality assessment of all randomized controlled trials that qualify for this particular subject matter, together with reported BC mortality in the screened vs. control population. In all, eight trials were analyzed (with the data provided for one that was excluded for unacceptable randomization bias), with a total of 600,000 participants. Raw data are given in the table below.
 
Vital
statistics
TRIAL   nadequate   ninadequate   nflawed
Age trial Canada Edinburgh Göteborg Malmö New York Stockholm Two county
Screened
Group
BC deaths

53,884
105

44,925
212

28,628
176

21,650
88

20,695
87

31,000
218

40,318
66

77,080
261
Controls
Group
BC deaths

106,956
251

44.908
213

26,015
187

29,961
162

20,783
108

31,000
262

19,943
45

55,985
277

Numbers are taken from the systematic (i.e. including all eligible trials on this particular outcome) review by researchers from the Nordic Cochrane center (Screening for breast cancer with mammography, Gøtzsche and Nielsen, 2001/2009/2011). There were several other systematic reviews of the trials on screening mammography and breast cancer mortality, but they typically did not assess trial quality, or were limited to the certain age groups.

In general, numbers reported by these trials are used in all of these reviews; the interesting part is how reliable are the sources of these numbers. Here's the summary.

MAMMOGRAPHY SCREENING TRIALS: EFFECT ON BC MORTALITY
(Based on: Nordic Cochrane Center systematic review 2009)
n Adequate (A)  n Unclear/Inadequate (B/C)  n Flawed (excluded)
 
# Trial Age BC deaths,
screened
vs.
controls
CRITERIA Class
Proper
randomization
No significant unbalanced exclusions No early systematic screening
of controls
Reliable cause-of-death assessment A
n
B
n
C
n

1
New York
1963
50+ 0.78 ? Ï1 P Ï2   n  
50- 0.78
All 0.83

2
Malmö
1976
50+ 0.86 P ?3 P ? n    
50- 0.52
All 0.81*

3
Two-Countya
1977
50+ 0.64 ? Ï Ï4 Ï5     n
50- 0.91
All 0.68

4
Edinburgh
1978
50+ 0.88 Ï6 Ï P Ï     n
50- 0.79
All 0.86

5
Canadab
1980
50+ 1.02 P P P P n    
50- 0.97
All 0.995

6
Stockholm
1981
50+ 0.64 Ï ? Ï Ï   n  
50- 0.96
All 0.73

7
Göteborg
1982a
50+ 0.83 ? ? Ï Ï   n  
50- 0.70
All 0.75

8
Age Trial
1991
50+ n/a P P P ?7 n    
50- 0.83
All 0.83
4
INADEQUATE
TRIALS
n
50+ 0.70 CRITERIA BRIEF:
• Proper randomization should ensure that the risk is evenly distributed between screened and control group
•  Significantly imbalanced exclusions from screened vs. control group during or after trial indicate possible bias or substandard randomization
• Early systematic screening of the control group (contamination) reduces the effect of intervention (i.e. contrast between groups) making the results less reliable due to insufficient trial duration
• Cause-of-death assessment blinded to group status is the basic - although not necessarily sufficient - requirement for reliable, unbiased classification of deaths in trial population
50- 0.80
All 0.75
3
ADEQUATE
TRIALS
n
50+ 0.94
50- 0.87
All 0.90
ALL 7
TRIALS
nn
50+ 0.77
50- 0.84
All 0.81
ALL-CANCER
MORTALITY
n 1.02
nn 0.99
ALL-CAUSE
MORTALITY
n 0.99
nn 0.99
*Pooled ratios are weighted  aKopparberg and Östergötland trials;  bCanada 1 and 2   
1 Estimated 853 women excluded from the screened vs. 336 from control group
2
Case-of-death assessment unblinded to group status for 72% of women
3
137 women from the baseline screened group and 26 from controls missing from later records
 
4
Control group screening started within 3-5y
5
Case-of-death assessment not blind to group status
6
Nearly twice as many women with highest socioeconomic status in the screened group
7
No information on autopsy rate; no independent cause-of-death assessment

What the inspection of trial data showed is that the lack of transparency or documentation (?) and/or documented sub-standard features in the design and execution (Ï) were rather common in these trials. Comments added at the bottom are only a small portion of inadequacies plaguing most of them, given to illustrate their nature and extent. 

How confident can we be of these studies reporting on the effect of screening on breast cancer mortality, with the "Reliable cause-of-death assessment" column having

a single clear O.K. mark?

A trial with the iconic status in pro-screening arguments was - and still is - the Swedish Two-County trial, the most likely reasons being that it reported the largest BC mortality reduction of all, and that it had the largest number of participants. Never mind that it only used a single-view mammography, with most of the screened women having no more than three mammograms altogether, and that its control group was subjected to screening within 3-5 years from the start.

Never mind that this flies in face of the general consensus that for the screening-related BC mortality reduction to start showing requires at least 5-year period, and up to several years more to reach its actual higher level (a pattern consistently documented in all other trials is that

BC mortality is actually higher in the screened group for at least first few years).

Never mind that a meta study of the Swedish trials found that the Two-County trial evidence disagrees with the Swedish official cause-of-death register in that it reported 10 BC deaths fewer in the screened group, and 27 more deaths in the controls (Nystrom 2002, to which Holmberg et al. - including lead trial author for the Two County L. Tabár - responded in 2009, "explaining" the discrepancy by a different cause-of-death criteria applied, and entirely ignoring the main point, that the sum of death cause re-classifications in the trial was in favor of screening in both, screened and control group).

Or that other studies found that the Two County trial's BC mortality reduction figures agree poorly with the reported cancer stages for the two groups (Zahl 2001), and that a large number of breast cancer cases and deaths in the official register seem to be missing from the trial data (Zahl 2006).

Or that the specifics of trial's randomization process haven't been published yet, despite it's been well over two decades since it ended. Its trial randomization is suspect, among other reasons, for its two joined sub-trials, in Kopparberg and Östergötland, reporting BC mortality rate in their respective control groups that

differs nearly by a factor of two

(0.21 vs. 0.12%, respectively). Or...

Chances are, this trial avoided exclusion so far only due to its iconic status used by the mighty proponents of screening mammography for its popularization; but it could be only a matter of time.

These serious inadequacies are in stark contrast with the characterization of Swedish mammography trials - and particularly the Two County - as the most reliable by the pro-screening side. And no less with its dismissal of the only trial that found no BCM reduction with screening at all - the Canadian trial - which is unquestionably of the superior quality in both design and execution. One of the many objections thrown at it was that women in the control group in the Canada-1 trial (40-49y of age)

were thought to perform breast self-examination.

That, according to the critics, resulted in the control and screening groups being not comparable anymore (that despite the critics at the same time generally maintaining that breast self-examination has no appreciable effect on BC mortality).

But those same critics apparently have no objections to the fact that screened women in the Two-County trial were encouraged to perform monthly self examination.

Summing it up, the number of trials that we can use with a reasonable confidence to look for indication of the effectiveness of screening on BC mortality reduction, shrinks to three. Their combined reduction rate for the screened populations is statistically insignificant (i.e. indistinguishable from variations due to chance)

10% for all women, 40-70y of age.

And it was below 10%, before the Malmo trial's unexpected upturn. The trial originally reported only 4% risk reduction ratio, which in the course of follow up grew to 19%. No other trial had nearly this magnitude of change in the reported rate. Facts that the trial's autopsy rate simultaneously declined from 3 in 4 to 1 in 3, and that blind to group status death-cause assessment was abandoned in favor of more bias/manipulation-prone open assessment, make the updated data less reliable (another problem with a long-term follow-up is that various forms of uncontrolled or uncontrollable contamination of the originally randomized groups creep in, randomly altering results of statistical analysis).

On the other hand, the four unreliable trials summed up significant, two and a half times higher BC mortality reduction - 25% - for the screened population.

All seven trials add up to 19% reduction over the follow-up period. This figure, however, is not viable in the context of reliability. As all pooled ratios in the review, it was obtained using weighted average concept (Mantel-Haenszel), which is based on trials' size and frequency of the outcome - not their design and execution quality. The 19% weighted average is somewhat higher than the arithmetic average (17.5%), due to more participants and outcomes (BC deaths) in the four inadequate studies, but reliability of data should be more important than mere quantity i.e. study size.

The researchers, Gøtzsche and Nielsen, probably had that in mind, putting out their estimate that what the data suggests is that screening probably reduces BC mortality, and that the

rate of reduction is likely to be about 15%.

This figure is nearly identical to that resulting from another recent independent systematic review of the trial evidence, by the United States Preventive Services Task Force (USPSTF). Based on the same RCTs reviewed by the Nordic Cochrane Center (with Edinburgh also excluded) for the 39-49 age group, it found 15% overall BCM rate reduction. For the 50-59 age group, data from six RCTs (New York excluded, and Age trial had no women 50y and over), the polled BCM reduction rate was 14% (Screening for Breast Cancer: An Update for the U.S. Preventive Services Task Force, Nelson et al. 2009).

Unlike the NCC review, which found most of the trials to be of low quality, the USPSTF review ranked them all as "fair". Thus there was no division on more and less reliable data sources. It is surprising, since among the top USPSTF criteria in evaluating trial quality are

proper randomization and blindness to status in the outcome assessment,

documented to be inadequate or lacking by the NCC in the trials they labeled as inadequate in their analysis - which is listed by the USPSTF among the top evidence resources quality-wise.

Realistically, it is probably more surprising that USPSTF went as far as it did over the line drawn by the overwhelmingly influential pro-screening camp, in setting the mortality reduction benefit due to screening at as "low" as 14-15% level, and by withdrawing its support for the routine screening of women younger than 50. The publication of USPSTF findings was followed by vitriolic reaction from the screening advocates, and its recommendations were rejected.

But, the truth is, the evidence reviewed in the Nordic Cochrane Center (NCC) and USPSTF studies, as incomplete, questionable and not applicable to the population at large, is the best we have. And the indication of BCM reduction benefit due to the screening based on it is probably too optimistic. Literally all these trials took place in the past century, some as far as 4-5 decades ago. Nowadays, with better informed women, higher standards of living, and advance in treatment efficiency, it is likely that the BCM reduction rate due to earlier detection is

lower than what it was decades ago.

But, is that really the best data that we can get from trials? Reasonable objection to these trials in general is the choice of main outcome: breast cancer mortality rate. Not only that the cause-of-death determination has been shown to be plagued with difficulties and bias - it is still only a part of the whole picture. The effect of X-ray mammography screening on the BCM rate is not the most important indicator; it is

the effect on overall mortality rate that should come first.

In other words, somewhat reduced breast cancer mortality cannot be considered beneficial, if it is offset, or even exceeded, by an increased treatment-related mortality from other causes. This rarely addressed, yet crucial question is addressed more closely on next page, for screened vs. unscreened women.

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