A fishing expedition is when a scientist initiates a large number of investigations simultaneously on the same data set. A good conceptual example is a study of the effect of a certain environmental chemical on cancer. A researcher could look for an association with bladder cancer, brain cancer, colon cancer, liver cancer, lung cancer, ovarian cancer, prostate cancer, skin cancer, and *that funny little thing hanging in the back of your throat* cancer. With so many different cancers to look at, the scientist is bound to find something worth publishing, even if the chemical is as harmless as table salt. It's like placing a single bet at a casino, but getting to spin the roulette wheel a couple dozen times.

The Bonferroni correction is a statistical adjustment for the multiple comparisons</strong> that are made in a fishing expedition. It effectively raises the standard of proof needed when a scientist looks at a wide range of hypotheses simultaneously.

The Bonferroni correction is quite simple. **If we are testing n outcomes instead of a single outcome, we divide our alpha level by n**. Suppose we were looking at the association of sodium chloride and 20 different types of cancers. Instead of testing at the tradition .05 alpha level, we would test at alpha=.05/20=.0025 level. This would ensure that the overall chance of making a Type I error is still less than .05.

You can also **apply the Bonferroni correction by adjusting the p-value**. A Bonferroni adjusted p-value would just be the normal p-value multiplied by the number of outcomes being tested. If the adjusted p-value ended up greater than 1.0, it would be rounded down to 1.0.

Some scientists dislike the use of the Bonferroni correction; they prefer instead that researchers clearly label any results from a fishing expedition as preliminary and/or exploratory. Furthermore, **the** **Bonferroni correction can cause a substantial loss in the precision** of your research findings.

### The global null hypothesis

Your general perspective on hypothesis testing is important. One perspective that clearly calls for a Bonferroni adjustment is a global null hypothesis.

Suppose that you are measuring a large number of outcome variables, and you will **conclude that a treatment is effective (or that an exposure is dangerous) if you find a statistically significant effect on ANY ONE one of your outcome variables**. So a new drug for asthma would be considered effective if it

- reduced the number of symptoms as measured by the number of wheezing episodes
- OR the number of emergency room visits related to asthma
- OR the number of patients who no longer required steroid treatment
- OR if the average patient had an improvement in lung capacity as measured by FEV1
- OR as measured by the FVC value
- OR as measured by the FEV1/FVC ratio
- OR as measured by the FEF25-75 value
- OR as measured by the PEFR value
- OR if the average patient had a better quality of life as measured by the SF-36.

When there is a clear global null hypothesis, then you should use a Bonferroni adjustment.

Consider a restrictive hypothesis, a conceptual hypothesis at the other extreme. Suppose that you will consider a treatment as effective only if it shows a statistically significant improvement in all of those outcome variables.

With a restrictive hypothesis, you might be justified in increasing your alpha level to .10 or .15 since your criteria for success is so stringent.

In truth most studies do not gravitate to either extreme, making it difficult for you to decide whether to use the Bonferroni adjustment.

### Designating primary outcome variables

When you need to examine many different outcome measures in a single research study, you still may be able to keep a narrow focus by specifying a small number of your outcome measures as primary variables. Typically, a researcher might specify 3-5 variables as primary. The fewer primary outcome variables, the better. You would then label as secondary those variables not identified as primary outcome variables.

When you designate a small number of primary variables, you are making an implicit decision. The success or failure of your intervention will be judged almost entirely by the primary variables. If you find that none of the primary variables are statistically significant, then you will conclude that the intervention was not successful. You would still discuss any significant findings among your secondary outcome variables, but these findings would be considered tentative and would require replication.

### Examining post hoc mechanisms

<blockquote>

<p>When some but not all of your outcome measures reach statistical significance, you should examine them for consistency with known mechanisms. In a study of male reproductive toxicology, some outcome measures are related to hormonal disruptions, others to incomplete sperm maturation, and still others to problems with the accessory sex glands.</p> <p>If the significant outcome variables all can be tied to a common mechanism, you have greater confidence in the research results. On the other hand, if each significant variable requires a different mechanistic explanation, you have less confidence. Also, if one outcome associated with a certain mechanism is significant and other outcomes associated with the same mechanism are not even approaching borderline significance, then you have less confidence in your findings.</p>

</blockquote> <p><strong>Other applications of the Bonferroni correction</strong></p> <blockquote>

<p>Another area where the Bonferroni correction becomes useful is with comparisons across multiple groups of subjects. If you have four treatment groups (e.g., A, B, C, and D), then there are six possible pairwise comparisons among these groups (A vs B, A vs C, A vs D, B vs C, B vs D, C vs D). If you are interested in all possible pairwise comparisons, the Bonferroni correction provides a simple way to ensure that making these comparisons does not lead to some of the same problems as testing multiple outcome measures.</p> <p>There are other approaches that work more efficiently than Bonferroni. Tukey's Honestly Significant Difference is the approach I prefer. But you also need to be sure that you are truly interested in ALL possible pairwise comparisons.</p>

</blockquote> <p><strong>Statistical versus practical significance</strong></p> <blockquote>

<p>Although all of the emphasis on this page has been on statistical significance, you should always evaluate practical significance as well. Suppose that among all your outcome measures, none shows an effect large enough to have any practical or clinical impact. In such a situation, discussion of whether to use a Bonferroni adjustment becomes meaningless.</p>

</blockquote> <p><b>Loss of power</b></p> <blockquote>

<p>Too many studies have an inadequate sample size, and the Bonferroni correction will make this problem even worse. If you apply a Bonferroni correction with a data set that is already too small, you are implicitly stating that it is important only to control the probability of a Type I error (rejecting the null hypothesis when the null hypothesis is true), and that you don't care about limiting the probability of a Type II error (accepting the null hypothesis when the null hypothesis is false). </p>

</blockquote> <p><strong>Examples</strong></p> <blockquote>

<p>In a study of Parkinson's disease (<a href="http://www.ncbi.nlm.nih.gov/entrez/query.fcgi?cmd=Retrieve&db=PubMed&list_uids=11687621&dopt=Abstract">Kaasinen 2001</a>), a group of 61 unmedicated Parkinson's disease patients and 45 healthy controls were compared on 22 separate personality scales. The was prior data to suggest that novelty seeking would be lower in patients with Parkinson's, so this comparison was made without any Bonferroni adjustments. The remaining personality scores, however, had no such prior information and a Bonferroni adjustment was used for these remaining scales. An additional analysis looked PET scans for a subset of 47 Parkinson's patients. The 18F-dopa uptake in 10 regions of the brain were correlated with the 22 personality traits. The correlations involving novelty seeking were not adjusted, but the remaining correlations were adjusted to account for the fact that 220 (10x22) correlations were being analyzed. A significant correlation was observed between harm avoidance and 18F-dopa uptake in the right caudate nucleus (r=0.53, corrected P = 0.04). Interestingly, there was not a statistically significant correlation in the left caudate nucleus (r=0.43, corrected P=0.88) even though the uncorrected p-value was less than 0.01.</p> <p>In a study of intraoperative hypothermia (<a href="http://www.ncbi.nlm.nih.gov/entrez/query.fcgi?cmd=Retrieve&db=PubMed&list_uids=12441007&dopt=Abstract">Janicki 2002</a>), 12 patients were randomized to a forced air warming system and 12 to a newly developed whole body water garment. The primary outcome, body core temperature, was measured at five times during the operation (<font class="bodytext" size="3">incision; 1 hr after incision; placement of liver graft into the recipient; reperfusion; and closing) and at three times after the operation (T=0, 1, or 2 hours in the ICU). The comparisons were adjusted by dividing the alpha level by 5 (for the intraoperative measures) or by 3 (for the postoperative measures). It would have been possible to perform a single Bonferroni correction across all eight measures; perhaps the authors felt that intraoperative and postoperative measurement represented distinct and separate comparisons.</font></p>

</blockquote> <p><strong>Summary</strong></p> <blockquote>

<p>A Bonferroni adjustment is used when there are multiple outcome measures, and there is concern about the possibility that the results might be perceived as being a fishing expedition. The Bonferroni comparison using an adjusted alpha level equal to the original alpha level (usually .05) divided by the number of outcome measures.</p>

</blockquote> <p><strong>Further reading</strong></p> <blockquote>

<p><b>Assessing cause and effect from trials: a cautionary note.</b> D. Howel, R. Bhopal. Control Clin Trials 1994: 15(5); 331-4. <a href="http://www.ncbi.nlm.nih.gov/entrez/query.fcgi?cmd=Retrieve&db=PubMed&list_uids=8001354&dopt=Abstract"> [Medline]</a> </p> <p><strong><a href="http://http://www.aghmed.fsnet.co.uk/bonf/bonf.html">Carlo Emilio Bonferroni</a></strong>. Michael Dewey. Accessed on 2003-10-14. http://www.aghmed.fsnet.co.uk/bonf/bonf.html</p> <p><b>Decision theoretic designs for Phase II clinical trials with multiple outcomes.</b> Nigel Stallard. Biometrics 1999: 55971-77. <a href="http://www.ncbi.nlm.nih.gov/entrez/query.fcgi?cmd=Retrieve&db=PubMed&list_uids=11315037&dopt=Abstract"> [Medline]</a> </p> <p><b>Do multiple outcome measures require p-value adjustment?</b> R. J. Feise. BMC Med Res Methodol 2002: 2(1); 8. <a href="http://www.ncbi.nlm.nih.gov/entrez/query.fcgi?cmd=Retrieve&db=PubMed&list_uids=12069695&dopt=Abstract"> [Medline]</a> <a href="http://www.biomedcentral.com/1471-2288/2/8">[Full text]</a> </p> <p><b>Empirical-Bayes adjustments for multiple comparisons are sometimes useful.</b> S. Greenland, J. M. Robins. Epidemiology 1991: 2(4); 244-51. <a href="http://www.ncbi.nlm.nih.gov/entrez/query.fcgi?cmd=Retrieve&db=PubMed&list_uids=1912039&dopt=Abstract"> [Medline]</a> </p> <p><b>False positive outcomes and design characteristics in occupational cancer epidemiology studies.</b> G. G. Swaen, O. Teggeler, L. G. van Amelsvoort. Int J Epidemiol 2001: 30(5); 948-54. <a href="http://www.ncbi.nlm.nih.gov/entrez/query.fcgi?cmd=Retrieve&db=PubMed&list_uids=11689501&dopt=Abstract"> [Medline]</a> </p> <p><strong><a href="http://www.bioinf.uni-hannover.de/~mcp2000/abstracts/abstr29.html"> Intersection-Union Procedures for Some Restricted Models</a></strong>. Yosef Hochberg, Michael C. Mosier. Accessed on 2000-7 June. www.bioinf.uni-hannover.de/~mcp2000/abstracts/abstr29.html</p> <p><b>Invited Commentary: Re: "Multiple Comparisons and Related Issues in the Interpretation of Epidemiologic Data".</b> John R. Thompson. American Journal of Epidemiology 1998: 147(9); 801-811. <a href="http://www.ncbi.nlm.nih.gov/entrez/query.fcgi?cmd=Retrieve&db=PubMed&list_uids=9583708&dopt=Abstract"> [Medline]</a> </p> <p><b>The Method of Multiple Working Hypotheses.</b> TC Chamberlin. The Scientific Monthly 1944: 59357 - 62. </p> <p><b>Methods of correcting for multiple testing: operating characteristics.</b> B. W. Brown, K. Russell. Statistics in Medicine 1997: 16(22); 2511-28. </p> <p><b>Multiple comparisons and related issues in the interpretation of epidemiologic data.</b> D. A. Savitz, A. F. Olshan. Am J Epidemiol 1995: 142(9); 904-8. <a href="http://www.ncbi.nlm.nih.gov/entrez/query.fcgi?cmd=Retrieve&db=PubMed&list_uids=7572970&dopt=Abstract"> [Medline]</a> </p> <p><b>Multiple Comparisons Theory and Methods.</b> Jason C. Hsu (1996) London: Chapman & Hall. </p> <p><strong> <a href="http://www.hms.harvard.edu/orsp/coms/BiosafetyResources/Statistics/Multiple_significance_tests_and_the_Bonferroni_correction.htm"> Multiple significance tests and the Bonferroni correction</a></strong>. Martin Bland. Accessed on 2002-11-29. www.hms.harvard.edu/orsp/coms/BiosafetyResources/<br> Statistics/Multiple_significance_tests_and_the_Bonferroni_correction.htm</p> <p><b>No adjustments are needed for multiple comparisons.</b> K. J. Rothman. Epidemiology 1990: 1(1); 43-6. <a href="http://www.ncbi.nlm.nih.gov/entrez/query.fcgi?cmd=Retrieve&db=PubMed&list_uids=2081237&dopt=Abstract"> [Medline]</a> </p> <p><b>Permutation Tests for Joinpoint Regression with Applications to Cancer Rates.</b> Hyune-Ju Kim, Michael P. Fay, Eric J. Feuer, Douglas N. Midthune. Statistics in Medicine 2000: 19(3); 335-351. </p> <p><b>Problems in defining cutoff points of continuous prognostic factors: example of tumor thickness in primary cutaneous melanoma.</b> P. Buettner, C. Garbe, I. Guggenmoos-Holzmann. Journal Clinical Epidemiology 1997: 50(11); 1201-10. <a href="http://www.ncbi.nlm.nih.gov/entrez/query.fcgi?cmd=Retrieve&db=PubMed&list_uids=9393376&dopt=Abstract"> [Medline]</a> </p> <p><b>Quantitative Evaluation of Multiplicity in Epidemiology and Public Health Research.</b> Kenneth J. Ottenbacher. American Journal of Epidemiology 1998: 147(7); 615-619. <a href="http://www.ncbi.nlm.nih.gov/entrez/query.fcgi?cmd=Retrieve&db=PubMed&list_uids=9554599&dopt=Abstract"> [Medline]</a> </p> <p><b>Simultaneous Statistical Inference Second Edition.</b> Rupert G. Miller (1981) New York: Springer-Verlag. </p> <p><b>Some comments on frequently used multiple endpoint adjustment methods in clinical trials.</b> A. J. Sankoh, M. F. Huque, S. D. Dubey. Stat Med 1997: 16(22); 2529-42. <a href="http://www.ncbi.nlm.nih.gov/entrez/query.fcgi?cmd=Retrieve&db=PubMed&list_uids=9403954&dopt=Abstract"> [Medline]</a> </p> <p><strong><a href="http://www.tufts.edu/~gdallal/multtest.htm">There must be something buried in here somewhere</a></strong>. Jerry Dallal. Accessed on 2003-05-15. www.tufts.edu/~gdallal/multtest.htm</p> <p><b>What's wrong with Bonferroni adjustments.</b> T. V. Perneger. British Medical Journal 1998: 316(7139); 1236-8. <a href="http://www.ncbi.nlm.nih.gov/entrez/query.fcgi?cmd=Retrieve&db=PubMed&list_uids=9553006&dopt=Abstract"> [Medline]</a> <a href="http://bmj.com/cgi/content/full/316/7139/1236">[Full text]</a></p>

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