DELINEAMENTO E PLANEJAMENTO - ecologia.ib.usp.brecologia.ib.usp.br/planeco/lib/exe/fetch.php?media=planeco:... · trent university, canada nÃo abordam delineamento e planejamento!!

DELINEAMENTOEPLANEJAMENTO

BIE5793-PrincípiosdePlanejamentoeAnálisedeDadosemEcologia

ETAPASDOMÉTODOCIENTÍFICO

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TrentUniversity,Canada

NÃOABORDAMDELINEAMENTOEPLANEJAMENTO!!

VÃODIRETODASHIPÓTESES/PREDIÇÕESPARAACOLETADEDADOS


MESMOQUANDOOESQUEMANÃOÉTRIVIAL

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DELINEAMENTO ANÁLISECOLETADEDADOS

PREDIÇÕES

QUANDOINCORPORA,PARECEUMPROCESSOSIMPLESELINEAR

MAS,DELINEAMENTOÉUMAETAPAIMPORTANTEECOMPLEXA

VariáveisOperacionais(p.ex.:discretaxcontínuas)

Tudodependedaperguntacientífica!

Premissas

COLETA ANÁLISEDELINEAMENTO

TamanhodeamostraDistribuiçãoespacialEsforçoamostralpossível

PORQUEDELINEAMENTOÉIMPORTANTE?"Designinganexperimentproperlywillnotonlyhelpyouinanalyzing

data–itmaydeterminewhetheryoucananalyzedataatall!"MichaelPalmer

INCERTEZASINTRÍNSECASDAPOPULAÇÃOESTATÍSTICA

VARIÁVEISALEATÓRIAS AMOSTRA

INCERTEZAS

INCERTEZASADICIONAISSOBREAQUALIDADEDAESTIMATIVADOSPARÂMETROSPOPULACIONAIS

DIFERENÇAENTREPARÂMETROSEESTIMADORES

Definidospeloselementosdas

unidadesamostraisouréplicas

http://oestatistico.com.br/

Desconhecidos,MasFIXOS

Importânciadedefinirclaramente

apopulação Estatísticaouestimativapontual

OQUEÉ,MATEMATICAMENTE,UMBOMESTIMADOR?

SEMVIÉS-Seforemtomadasmedidasdeváriasamostrascomesseestimador,amédiadessasmedidasdevecoincidircomoparâmetrooriginal

CONSISTENTE-Quantomaisaumentarotamanhodaamostra,ovalorconvergeparaoparâmetrooriginaleavariânciadiminui

EFICIENTE-Dentreosdiferentesestimadores,dadoummesmotamanhodeamostra,omaiseficienteseráoqueapresentarmenorvariância

DEFINIÇÃOBASEADAEMPROCEDIMENTOSMATEMÁTICOSE/OUCOMPUTACIONAIS

NÃOSEPREOCUPEMCOMISSO!!

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MédiaeVariânciadaAMOSTRAsãobonsestimadoresdaMédiaeVariânciadaPOPULAÇÃO

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NOSSOOBJETIVO:Obterumaestimativaconfiávelcomomenoresforçoamostral

P.ex.:pontuaçãomédia

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SEMVIÉS-Ovalorobtidocomaamostraestatísticadeveserigualaoparâmetro.Nãodevesubestimarousuperestimaroparâmetropopulacional

PRECISA-Amaiorpartedosvaloresobtidosnaamostra,deveestarnasproximidadesdoparâmetropopulacional(ERROSPEQUENOS)

UMBOMDELINEAMENTO

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OQUEÉUMBOMDELINEAMENTO?

Dependedaperguntacientífica!!!

Mas,podemosajudar...

Trabalhandoumexemplohipotético...

Objetivoinicial:Estimaronúmeromédiodesementesproduzidasporessaespécie

Estamosinteressadosemmodelarasrespostasreprodutivasdeumaespécieraradeplantavisandoassegurarsuamanutençãoa

longoprazo

Algumasinformaçõesprévias:

-Aespécieocorrenaspartesmaisaltasdeumacadeiademontanhas

-Aespécieégeograficamenterara,maslocalmenteabundante

-Éumaespécietípicadesub-bosque

-Possuiumfármacodeimportânciacomercial

-Aindanãosabemosquasenadadessaespécie

OceanoAtlântico-Leste(E)

Oeste(W)

Sul(S) Norte(N)

Vocêtemrecursosparafazer10unidadesamostrais(parcelasde50x50m).ConsiderandoapaisagemabaixoeascaracterísticasindicadasanteriormenteIndiquenafigura,com"x",comoalocariaasUAs.


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Vocêtemrecursosparafazer60unidadesamostrais(parcelasde20x20m).Indiquenafiguracom"o",comoalocariaasUAs.

Parabéns!!!Vocêacabadereceberumfinanciamento!!

VIÉS

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that we can only draw conclu-sions about the populationfrom which we have taken arandom sample. If our plots ona mud flat were scattered overa 20 m!20 m area, then ourconclusions only apply to thatarea; if we used a particularstrain of rats, then we haveonly a conclusion about that genetic strain, and soon.

The second aspect of randomization concernsthe allocation of treatments to experimentalunits or vice versa. One of the standard recom-mendations in experimental design is that theexperimental units be randomly allocated totreatment groups. This means that no pattern oftreatments across experimental units is subjec-tively included or excluded (Mead 1988) andshould ensure that systematic differencesbetween experimental units that might confoundour interpretation of treatment effects are mini-mized (Hurlbert 1984, Underwood 1997). The cray-fish example described at the beginning ofSection 7.2 is an illustration, if somewhat con-trived, of the problem.

An artificial example, analogous to onedescribed by Underwood (1997), involves anexperiment looking at the difference in growthrates of newly hatched garden snails fed either theflowers or the leaves of a particular type of plant.The flowers are only available for a short period oftime, because the plant flowers soon after rain.When the flowers are available, we feed it to anysnails that hatch over that period. Snails thathatch after the flowering period are given theleaves of the plant. The obvious problem here isthat the two groups of snails may be inherentlydifferent because they hatched at different times.Snails that hatch earlier may be genetically differ-ent from snails that hatch later, have had differ-ent levels of yolk in their eggs, etc. Our results may

reflect the effect of diet, or they may reflect differ-ences in the snails that hatch at different times,and these two sources of variation are con-founded. Clearly, we should take all the snails thathatch over a given period, say the floweringperiod, and give some of them flowers and othersleaves to eat.

The allocation of experimental units to treat-ments raises the difficult issue of randomizationversus interspersion (Hurlbert 1984). Reconsiderthe experiment described earlier on the effects offish predation on marine benthic communities.Say we randomly choose ten plots on an intertidalmudflat and we randomly allocate five of these asfish exclusion (E) plots and five as cage-control (C)plots. What do we do if, by chance, all the controlplots end up higher on the shore than all theexclusion plots (Figure 7.2)? Such an arrangementwould concern us because we really want ourtreatment and control plots to be interspersed toavoid confounding fish effects with spatial differ-ences such as tidal height. The simplest solution ifwe end up with such a clumped pattern after aninitial randomization is to re-randomize – anyother pattern (except the complete reverse with allcontrol plots lower on the shore) will incorporatesome spatial interspersion of treatments and con-trols. However, we must decide a priori whatdegree of spatial clumping of treatments is unac-ceptable; re-randomizing until we get a particularpattern of interspersion is not really randomiza-tion at all.

Why not guarantee interspersion by arranging

162 DESIGN AND POWER ANALYSIS

Figure 7.2. Possible result ofrandom allocation of ten plots on anintertidal mudflat to two treatments– fish exclusion (E) and cage-control(C).

Nesseexemplo,a"distânciaatéaágua"nãofoiconsideradanaanálise

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Tratamento

Controle

FATORESDECONFUSÃO

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likely to have males andfemales. Unfortunately, pos-sible confounding is rarelythis obvious and confounding can sneak into anexperimental design in many ways, especiallythrough inappropriate replication, lack of propercontrols and lack of randomized allocation ofexperimental units to treatments. These issueswill be our focus in this chapter.

Sometimes, confounding is a deliberate part ofexperimental design. In particular, when we havetoo many treatment combinations for thenumber of available replicate units, we might con-found some interactions so we can test maineffects (Chapter 9). Designs with such deliberateconfounding must be used with care, especially inbiology where interactive effects are common anddifficult to ignore.

7.2.1 ReplicationReplication means having replicate observationsat a spatial and temporal scale that matches theapplication of the experimental treatments.Replicates are essential because biologicalsystems are inherently variable and this is partic-ularly so for ecological systems. Linear modelanalyses of designed experiments usually rely oncomparing the variation between treatmentgroups to the inherent variability between experi-mental units within each group. An estimate ofthis latter variability requires replicate units.

Replication at an appropriate scale also helpsus avoid confounding treatment differences withother systematic differences between experimen-tal units. For example, to test if there are effects offish predation on the abundance of a species ofbivalve on intertidal mudflats, we might set up afield experiment using fish exclusion cages andsuitable cage controls (see Section 7.2.2 for discus-sion of controls) over plots (experimental units)on the mudflat. If we simply have a single exclu-sion plot and a single control plot, then the effectsof our treatment (fish exclusion) are confounded

with inherent differences between the two plotsrelated to their spatial location, such as tidalheight, sediment composition, etc. With two ormore replicate plots for each of the two treat-ments (exclusion and control), we can be muchmore confident in attributing differencesbetween treatment and control plots to fish exclu-sion rather than inherent plot differences. Notethat replication does not guarantee protectionfrom confounding because it is still possible that,by chance, all our treatment plots are differentfrom our control plots in some way besides accessto fish. However, the risk of confounding isreduced by replication, especially when combinedwith randomized allocation of treatments toexperimental units (Section 7.2.3).

While most biologists are well aware of theneed for replication, we often mismatch the scaleof those replicates relative to treatments beingapplied. Probably no other aspect of experimentaldesign causes more problems for biologists(Hurlbert 1984). Imagine a study designed to testthe effects of fire on the species richness of soilinvertebrates. Fire is difficult to manipulate in thefield, so investigators often make use of a naturalwildfire. In our example, one burnt area might belocated and compared to an unburnt area nearby.Within each area, replicate cores of soil are col-lected and the species richness of invertebratesdetermined for each core (Figure 7.1). The meannumber of species of invertebrates between thetwo areas was compared with a t test, after verify-ing that the assumptions of normality and equalvariances were met.

There is nothing wrong with the statistical testin this example. If the assumptions are met, a t testis appropriate for testing the H0 that there is nodifference in the mean number of invertebratespecies between the two areas. The difficulty isthat the soil cores are not the appropriate scale of


Figure 7.1. Example of aninappropriately replicated study onthe effects of fire on soilinvertebrates. Each area is sampledwith five replicate soil cores.

UnidadesamostraistomadasemumaescalaeinferênciafeitaemoutraescalaNãosãoréplicasverdadeiras(sãosub-amostras)enãosãoindependentes

Quaissãoasunidadesamostraisnoexemploacima?

Qual(is)pergunta(s)poderia(m)serrespondida(s)comosdadosobtidosnesseestudo?

Círculocinza=pontodeamostragemdebiomassademicro-organismosdesolo

SERIAUMAPSEUDORREPLICAÇÃOSEAPERGUNTAFOSSE:"Áreassujeitasafogotêmmenorbiomassademicro-organismosnosolo?"

Asunidadesamostraissãoosquadrados(n=1emcadacondição)eoscírculossãosub-amostras

likely to have males andfemales. Unfortunately, pos-sible confounding is rarelythis obvious and confounding can sneak into anexperimental design in many ways, especiallythrough inappropriate replication, lack of propercontrols and lack of randomized allocation ofexperimental units to treatments. These issueswill be our focus in this chapter.

Sometimes, confounding is a deliberate part ofexperimental design. In particular, when we havetoo many treatment combinations for thenumber of available replicate units, we might con-found some interactions so we can test maineffects (Chapter 9). Designs with such deliberateconfounding must be used with care, especially inbiology where interactive effects are common anddifficult to ignore.

7.2.1 ReplicationReplication means having replicate observationsat a spatial and temporal scale that matches theapplication of the experimental treatments.Replicates are essential because biologicalsystems are inherently variable and this is partic-ularly so for ecological systems. Linear modelanalyses of designed experiments usually rely oncomparing the variation between treatmentgroups to the inherent variability between experi-mental units within each group. An estimate ofthis latter variability requires replicate units.

Replication at an appropriate scale also helpsus avoid confounding treatment differences withother systematic differences between experimen-tal units. For example, to test if there are effects offish predation on the abundance of a species ofbivalve on intertidal mudflats, we might set up afield experiment using fish exclusion cages andsuitable cage controls (see Section 7.2.2 for discus-sion of controls) over plots (experimental units)on the mudflat. If we simply have a single exclu-sion plot and a single control plot, then the effectsof our treatment (fish exclusion) are confounded

with inherent differences between the two plotsrelated to their spatial location, such as tidalheight, sediment composition, etc. With two ormore replicate plots for each of the two treat-ments (exclusion and control), we can be muchmore confident in attributing differencesbetween treatment and control plots to fish exclu-sion rather than inherent plot differences. Notethat replication does not guarantee protectionfrom confounding because it is still possible that,by chance, all our treatment plots are differentfrom our control plots in some way besides accessto fish. However, the risk of confounding isreduced by replication, especially when combinedwith randomized allocation of treatments toexperimental units (Section 7.2.3).

While most biologists are well aware of theneed for replication, we often mismatch the scaleof those replicates relative to treatments beingapplied. Probably no other aspect of experimentaldesign causes more problems for biologists(Hurlbert 1984). Imagine a study designed to testthe effects of fire on the species richness of soilinvertebrates. Fire is difficult to manipulate in thefield, so investigators often make use of a naturalwildfire. In our example, one burnt area might belocated and compared to an unburnt area nearby.Within each area, replicate cores of soil are col-lected and the species richness of invertebratesdetermined for each core (Figure 7.1). The meannumber of species of invertebrates between thetwo areas was compared with a t test, after verify-ing that the assumptions of normality and equalvariances were met.

There is nothing wrong with the statistical testin this example. If the assumptions are met, a t testis appropriate for testing the H0 that there is nodifference in the mean number of invertebratespecies between the two areas. The difficulty isthat the soil cores are not the appropriate scale of


Figure 7.1. Example of aninappropriately replicated study onthe effects of fire on soilinvertebrates. Each area is sampledwith five replicate soil cores.

Círculocinza=pontodeamostragemdebiomassademicro-organismosdesolo

NÃOSERIAUMAPSEUDORREPLICAÇÃOSEAPERGUNTAFOSSE:

"Essaáreasujeitaafogotemmenorbiomassademicro-organismosnosolodoqueessaoutraáreanãosujeitaafogo?"

Nessecaso:asunidadesamostraisseriamoscírculos(n=5emcadaárea)

PORÉM,INFERÊNCIARESTRITA-VALEAPENA?

204 STUART H. HURLBERT Ecological MonographsVol. 54, No. 2

A SIMPLE PSEUDOREPLICATION

B. SACRIFICIAL PSEUDOREPLICATION

Xl x2 91 Y2 x3 kl $3 94

C. TEMPORAL PSEUDOREPLICATION?l 72 &3 Kl

time

FI G. 5. Schematic representation of the three most com-mon types of pseudoreplication. Shaded and unshaded boxesrepresent experimental units receiving different treatments.Each dot represents a sample or measurement. Pseudorepli-cation is a consequence, in each example, of statistically test-ing for a treatment effect by means of procedures (e.g.,-l test,U test) which assume, implicitly, that the four data for eachtreatment have come from four independent experimentalunits (=treatment replicates).

where only a single control area and single impact areaare available.

One example Green uses is that of wastes being dis-charged into a river. If it is possible to take replicatesamples both upstream (control area) and downstreamfrom the discharge point and to do this both beforeand after the discharging of wastes begins, Green sug-gests carrying out what he terms an “optimal impactstudy.” Once the data are gathered, he recommendsthat some procedure such as analysis of variance beapplied and that “the evidence for impact effects is asignificant areas-by-times interaction” (p. 70). I wouldargue that this is improper, and that the best one cando in such a situation is to develop graphs and tablesthat clearly show both the approximate mean valuesand the variability of the data on which they are based.

Though the statistical procedure (ANOVA) recom-mended by Green is more sophisticated than the I tests,U tests, and x2 tests used in most of the earlier studiescited for pseudoreplication (Table 3), pseudoreplica-tion is no less the result. The ANOVA can only dem-onstrate significant differences between locations, notsignificant effects of the discharge. Since the treatmentscannot be interspersed or assigned randomly to exper-imental plots (the several sampling sites, both up-stream and downstream), the experiment is not con-trolled except in a subjective and approximate way.

More specifically, the “areas-by-times interaction”can be interpreted as an impact effect onZy if we assumethat the differences between upstream and downstreamlocations will remain constant over time if no wastes

are discharged or if they are without effect. This isunreasonable. The magnitude of the true differences(Ap) between two “similar” segments of a river, or two“similar” ponds, or two “similar” field plots changesconstantly over time.

If ANOVA were appropriate, we would have to makearbitrary decisions about how to measure difference.For example, upstream mayfly density is Xu and down-stream mayfly density is &. Should our null hypothesisby that (XJ&) will not change with time, or should itbe that (Xu - &) will not change? (Eberhardt [ 1976:331 suggests the former.) Or is some other measure ofdifference more appropriate? Different proceduresprobably would be appropriate for different kinds ofvariables.

Eberhardt (1976, 1978) addresses this same problemof how to assess impact when there is a single siteexposed. His conclusions are similar to those of Green(1979), in that he acknowledges the before-after, up-stream+lownstream sampling study to be the bestavailable option. However, Eberhardt offers many ca-veats, clearly states the statistical difficulty, and inventsthe properly pejorative terms “pseudoexperiment” and“pseudodesign” for the procedure. In his own words:

What cannot presentZy be done is to insure thatclassical inferential methods can actually be appliedto pre- and post-operational data on one impactedsite [1976:321] . . . . The whole formal technology ofexperimental design is not properly admissible [ I 978:2101. . . . [Such work] is really more in the area ofsample survey design than a part of the design ofexperiments [I9761321 . . . . We have as yet not pro-gressed very far in trying to carry the pseudodesignidea to an operationally eflective stage. I am not evensure that goal is either feasible or desirable [1976:351.

As examples of first-rate “optimal impact studies”may be cited the Hubbard Brook deforestation exper-iment (e.g., Likens et al. 1970, 1977) and the Canadianwhole-lake fertilization experiments (e.g., Schindler etal. 197 1, Schindler 1974). Replicate experimental unitswere not used in these investigations, yet the effects ofthe experimental variables were convincingly dem-onstrated. Inferential statistics were not used (with mi-nor exceptions). They were not applicable, and theywould not have made the results any clearer or theconclusions any firmer. All experimenters who do notor cannot employ true replication would do well toemulate the straightforwardness of these two outstand-ing research groups.

Temporal pseudoreplicationThis differs from simple pseudoreplication only in

that the multiple samples from each experimental unitare not taken simultaneously but rather sequentiallyover each of several dates (Fig. 5C). Dates are thentaken to represent replicated treatments and signifi-

MASnãopodemsertratadascomoréplicasindependentes!->Correçãoanalítica

EMGERAL,ÉMELHORINVESTIREMMAISUNIDADESAMOSTRAIS(RÉPLICAS)DOQUEEMSUB-AMOSTRAS

PSEUDORREPLICAÇÃO

Sub-amostrasaumentamaprecisãodeumaestimativa

Ecological Monographs 54(2), 1984,pp. 187-2~$3 1984 by the Ecological Society of America

11

PSEUDOREPLICATION AND THE DESIGN OF ECOLOGICALFIELD EXPERIMENTS

S T U A R T H. HURLBERTDepartment of Biology, San Diego State University,

San Diego, California 92182 USA

Abstract. Pseudoreplication is defined. as the use of inferential statistics to test for treatment effectswith data from experiments where either treatments are not replicated (though samples may be) orreplicates are not statistically independent. In ANOVA terminology, it is the testing for treatmenteffects with an error term inappropriate to the hypothesis being considered. Scrutiny of 176 experi-mental studies published between 1960 and the present revealed that pseudoreplication occurred in27% of them, or 48% of all such studies that applied inferential statistics. The incidence of pseudo-replication is especially high in studies of marine benthos and small mammals. The critical featuresof controlled experimentation are reviewed. Nondemonic intrusion is defined as the impingement ofchance events on an experiment in progress. As a safeguard against both it and preexisting gradients,interspersion of treatments is argued to be an obligatory feature of good design. Especially in smallexperiments, adequate interspersion can sometimes be assured only by dispensing with strict random-ization procedures. Comprehension of this conflict between interspersion and randomization is aidedby distinguishing pre-layout (or conventional) and layout-specifit alpha (probability of type I error).Suggestions are offered to statisticians and editors of ecological j oumals as to how ecologists’ under-standing of experimental design and statistics might be improved.

Key words: experimental design; chi-square; R. A. Fisher; W. S. Gossett; interspersion of treat-ments; nondemonic intrusion; randomization; replicability; type I error.

No one would now dream of testing the response to a treat-ment by comparing two plots, one treated and the other un-treated.

-R. A. Fisher and J. Wishart (1930)

. . . field experiments in ecology [usually] either have noreplication, or have so few replicates as to have very little sen-sitivity . . .

-L. L. Eberhardt (1978)

I don’t know how anyone can advocate an unpopular causeunless one is either irritating or ineffective.

-Bertrand Russell (in Clark 1976:290)

INTRODUCTION

The following review is a critique of how ecologistsare designing and analyzing their field experiments. Itis also intended as an exploration of the fundamentalsof experimental design. My approach will be: (1) todiscuss some common ways in which experiments aremisdesigned and statistics misapplied, (2) to cite a largenumber of studies exemplifying these problems, (3) topropose a few new terms for concepts now lackingconvenient, specific labels, (4) to advocate treatmentinterspersion as an obligatory feature of good design,and (5) to suggest ways in which editors quickly canimprove matters.

Manuscript received 25 February 1983; revised 2 1 June1983; accepted 25 June 1983.

Most books on experimental design or statistics cov-er the fundamentals I am concerned with either not atall or only briefly, with few examples of misdesignedexperiments, and few examples representing experi-mentation at the population, community or ecosystemlevels of organization. The technical mathematical andmechanical aspects of the subject occupy the bulk ofthese books, which is proper, but which is also dis-tracting to those seeking only the basic principles. Iomit all mathematical discussions here.

The citing of particular studies is critical to the hoped-for effectiveness of this essay. To forego mention ofspecific negative examples would be to forego a pow-erful pedagogic technique. Past reviews have been toopolite and even apologetic, as the following quotationsillustrate:

There is much room for improvement in field ex-perimentation. Rather than criticize particular in-stances, I will outline my views on the proper meth-ods . . . . (Connell 1974)

In this review, the writer has generally refrainedfrom criticizing the designs, or lack thereof, of thestudies cited and the consequent statistical weaknessof their conclusions; it is enough to say that the ma-jority of the studies are defective in these respects.(Hurlbert 1975)

. . . as I write my comments, I seem to produceonZy a carping at details that is bound to have thetotaZ effect of an ill-tempered scolding . . . . I hopethose whose work I have referenced as examples w i l l

On misinterpretations of pseudoreplication and related matters: areply to Oksanen

Stuart H. Hurlbert, Stuart H. Hurlbert, Dept of Biology and Center for Inland Waters, San Diego State Univ., SanDiego, California 92182, USA. ([email protected])

Pseudoreplication has become a widely accepted label for acertain class of statistical error common in the literature ofecology as well as of other fields. A wide-ranging critique by L.Oksanen recently published in this journal criticizes the term andconcept and concludes it to be a ‘‘pseudoissue,’’ one reflecting anintellectual disease, ‘‘a totally outdated epistemology’’ known as‘‘inductionism.’’ The present article addresses some of Oksanen’scomplaints. His critique is based on a misconception ofpseudoreplication, reflects unawareness of most of the literatureon the topic, and mistakenly argues that the seriousness of theerror is a function of whether an experiment is conducted in aninductive or deductive spirit. Oksanen’s advocacy of usingresources available for large scale ecology more for largenumbers of experiments with unreplicated treatments than forfewer experiments with modest replication of treatments isunrealistic. It is based on an overly optimistic view of the abilityof a meta-analysis to compensate for deficiencies, such as verynoisy estimates of treatment effects, of the individual studies thatare fed into it. A definition is offered of the term manipulativeexperiment, since adequate ones are lacking in the literature.Attention is called to the fact that for certain types ofmanipulative experiments lacking treatment replication, thereare valid ways to test for treatment effects.

Authors who cite Hurlbert would do better if they had readhis paper!

!/ A.J. Underwood (1998:344)

Twenty years ago I wrote a review of a particularcategory of statistical error that I termed pseudoreplica-tion, assessed the frequency with which it occurred inarticles reporting ecological field experiments, andcommented on related issues of experimental designand statistical analysis (Hurlbert 1984). Since that timethe term pseudoreplication has become widely used, andmany ecologists have become more aware of the need forclose concordance of design, analysis, and interpretationof experiments. A wide-ranging recent paper titled‘‘Logic of experiments in ecology: is pseudoreplicationa pseudoissue?’’ (Oksanen 2001) finds many faults of

logic and epistemology in my 1984 paper, and answersthe question in its title in the affirmative.If indeed pseudoreplication is a ‘‘pseudoissue’’, that

will be a shock to the American Statistical Association,which awarded the original pseudoreplication paper the

G.W. Snedecor Award for the best paper in biometry in1984.The present report responds to key points in Oksa-

nen’s (2001) critique but does not attempt to cover manycollateral issues he discusses. I focus in particular on hismisunderstanding of the nature of pseudoreplicationand experiments, his crediting of me with the revival of‘‘long dead’’ epistemologies, and his over-valuation of

the statistical treatment of experiments lacking treatmentreplication.While the present report was under review, Cottenie

and De Meester (2003) also published a critique ofOksanen’s (2001) key claims, reinforcing many pointsthat will be made here.There has been much published on pseudoreplication

since 1984 (Machlis et al. 1985, Hairston 1989, Krebs1989, Kroodsma 1989a, b, 1990, Hurlbert and White1993, Heffner et al. 1996, Lombardi and Hurlbert 1996,Garcıa-Berthou and Hurlbert 1999, Jenkins 2002, Hurl-bert and Meikle 2003). One of the best recent texts onexperimental design devotes several pages to discussingvarious types of pseudoreplication, though without us-ing the label (Mead 1988:107-122; reviewed in Hurlbert

1990). In its 1995 edition, one of the most widely usedstatistics texts quietly removed an example wherepseudoreplication had long been advocated in earliereditions as the correct way of doing things (Sokal andRohlf 1969:438, 1981:488, 1995). The problematic as-pects of Oksanen (2001) derive in part from its attemptto critique the concept of pseudoreplication whileignoring most of the literature on it.

O NP OI IN

I IP O

O N

Opinion is intended to facilitate communication between reader and author and reader andreader. Comments, viewpoints or suggestions arising from published papers are welcome.Discussion and debate about important issues in ecology, e.g. theory or terminology, mayalso be included. Contributions should be as precise as possible and references should bekept to a minimum. A summary is not required.

OIKOS 104:3 (2004) 591

2004,alutacontinua...

PSEUDORREPLICAÇÃO


AnalíticoSM

AnalíticoCM

Experimentos


AnalíticoSM

AnalíticoCM

Experimentos


Oeste(W)

Sul(S) Norte(N)

Vocêidentificapotenciaisproblemasnaamostragemanteriorquerealizou?

Gostariaderealocarsuasunidadesamostrais?

DELINEAMENTOSPARAESTUDOSOBSERVACIONAIS(nãoexclusivamente)

AMOSTRAGEMALEATÓRIASIMPLES

PRINCÍPIOBÁSICO:Qualquerunidadeamostraldeveteramesmaprobabilidadedeseramostrada

DEFINIRCLARAMENTEAPOPULAÇÃO(*)(limitesespaciaisetemporais)

DEFINIRAFORMADEALEATORIZAÇÃO(*)

DEFINIRUNIDADESAMOSTRAIS(*)

(*)importanteparatodosospróximosdelineamentos

PROCEDIMENTOS:

"Someinvestigatorslocateplotsbythrowingarockoveryourshoulder,orwalkingacertainnumberofstepswiththeireyesclosed.Notonlyaresuchtechniquesdangerous,theyalsodonotrepresentrandomsampling.Wecallsuchtechniques‘haphazard’."MichaelPalmer

ALEATORIZAÇÃO

Muitosmétodosinadequados(nãoatendemaspremissasdaaleatoriedade):-Atirarpedrasououtrosobjetosparatrás-Ircontandoepedirparaalguémdizerparaparar-Sortearumpontox;yeamostrarindivíduomaispróximo

ALEATORIZAÇÃO

Algunsmétodosadequados:-Tabeladenúmerosaleatórios-Númerosaleatóriosgeradosporprogramasdecomputador(ressalvas)-Últimosdígitosdecronômetro

SEFOIPOSSÍVELSEGUIRTODOSOSPROCEDIMENTOSINDICADOS:

MÉDIAAMOSTRAL=MÉDIAPOPULACIONAL

VANTAGENS:

(n-1)éusadoaoinvésdenparacorrigiroestimador

gradually from the middle of the sample andincorporate a measure of variability in the estima-tion procedure. They include the Huber M-estimator and the Hampel M-estimator, which usedifferent functions to weight the observations.They are tedious to calculate, requiring iterativeprocedures, but maybe useful when outliers arepresent because they downweight extreme values.They are not commonly used but do have a role inrobust regression and ANOVA techniques for ana-lyzing linear models (regression in Chapter 5 andANOVA in Chapter 8).

Finally, R-estimators are based on the ranks ofthe observations rather than the observationsthemselves and form the basis for many rank-based “non-parametric” tests (Chapter 3). The onlycommon R-estimator is the Hodges–Lehmann esti-mator, which is the median of the averages of allpossible pairs of observations.

For data with outliers, the median andtrimmed or Winsorized means are the simplest tocalculate although these and M- and R-estimatorsare now commonly available in statistical software.

2.2.2 Spread or variabilityVarious measures of the spread in a sample areprovided in Table 2.1. The range, which is the dif-ference between the largest and smallest observa-tion, is the simplest measure of spread, but thereis no clear link between the sample range andthe population range and, in general, the rangewill rise as sample size increases. The sample var-iance, which estimates the population variance,is an important measure of variability in manystatistical analyses. The numerator of theformula is called the sum of squares (SS, the sumof squared deviations of each observation fromthe sample mean) and the variance is the averageof these squared deviations. Note that we mightexpect to divide by n to calculate an average, butthen s2 consistently underestimates !2 (i.e. it isbiased), so we divide by n" 1 to make s2 an unbi-ased estimator of !2. The one difficulty with s2 isthat its units are the square of the original obser-vations, e.g. if the observations are lengths inmm, then the variance is in mm2, an area not alength.

16 ESTIMATION

Table 2.1 Common population parameters and sample statistics

Parameter Statistic Formula

Mean (l) y

Median Sample median y(n # 1)/2 if n odd(yn/2# y(n/2)# 1)/2 if n even

Variance (r 2) s2

Standard deviation (r) s

Median absolute deviation (MAD) Sample MAD median[ |yi" median| ]

Coefficient of variation (CV) Sample CV $ 100

Standard error of y (r y) s y

95% confidence interval for l y" t0.05(n" 1) % l% y# t0.05(n" 1)

s!n

s!n

s!n

sy

!"n

i& 1 (yi " y)2

n" 1

"n

i& 1 (yi " y)2

n" 1

"n

i& 1yi

n

gradually from the middle of the sample andincorporate a measure of variability in the estima-tion procedure. They include the Huber M-estimator and the Hampel M-estimator, which usedifferent functions to weight the observations.They are tedious to calculate, requiring iterativeprocedures, but maybe useful when outliers arepresent because they downweight extreme values.They are not commonly used but do have a role inrobust regression and ANOVA techniques for ana-lyzing linear models (regression in Chapter 5 andANOVA in Chapter 8).

Finally, R-estimators are based on the ranks ofthe observations rather than the observationsthemselves and form the basis for many rank-based “non-parametric” tests (Chapter 3). The onlycommon R-estimator is the Hodges–Lehmann esti-mator, which is the median of the averages of allpossible pairs of observations.

For data with outliers, the median andtrimmed or Winsorized means are the simplest tocalculate although these and M- and R-estimatorsare now commonly available in statistical software.

2.2.2 Spread or variabilityVarious measures of the spread in a sample areprovided in Table 2.1. The range, which is the dif-ference between the largest and smallest observa-tion, is the simplest measure of spread, but thereis no clear link between the sample range andthe population range and, in general, the rangewill rise as sample size increases. The sample var-iance, which estimates the population variance,is an important measure of variability in manystatistical analyses. The numerator of theformula is called the sum of squares (SS, the sumof squared deviations of each observation fromthe sample mean) and the variance is the averageof these squared deviations. Note that we mightexpect to divide by n to calculate an average, butthen s2 consistently underestimates !2 (i.e. it isbiased), so we divide by n" 1 to make s2 an unbi-ased estimator of !2. The one difficulty with s2 isthat its units are the square of the original obser-vations, e.g. if the observations are lengths inmm, then the variance is in mm2, an area not alength.

16 ESTIMATION

Table 2.1 Common population parameters and sample statistics

Parameter Statistic Formula

Mean (l) y

Median Sample median y(n # 1)/2 if n odd(yn/2# y(n/2)# 1)/2 if n even

Variance (r 2) s2

Standard deviation (r) s

Median absolute deviation (MAD) Sample MAD median[ |yi" median| ]

Coefficient of variation (CV) Sample CV $ 100

Standard error of y (r y) s y

95% confidence interval for l y" t0.05(n" 1) % l% y# t0.05(n" 1)

s!n

s!n

s!n

sy

!"n

i& 1 (yi " y)2

n" 1

"n

i& 1 (yi " y)2

n" 1

"n

i& 1yi

n


VARIÂNCIAAMOSTRAL=VARIÂNCIAPOPULACIONAL

TESTESDEHIPÓTESESPODEMSERREALIZADOSCOMSEGURANÇA

DESVANTAGENSEPROBLEMAS:

-REQUERUMTAMANHOGRANDEDEAMOSTRA

-ACESSOAOSPONTOSDEFINIDOS


-SEHOUVERHETEROGENEIDADE,AMBIENTESRAROSPODEMNÃOSERAMOSTRADOS

-MUITOESFORÇOQUANDOOBJETOSESTÃOAGREGADOSOUSÃORAROS(localmente)

SOLUÇÕES:

-ESTUDOPILOTOEBUSCAPORCONHECIMENTOSPRÉVIOS-ANALÍTICAS(ProcedimentosdeMonteCarlo)-MEDIÇÕESADICIONAIS(PARAEVITARFATORESDECONFUSÃO;PÓS-ESTRATIFICAÇÃO)-OPÇÃOPOROUTROSESQUEMASDEAMOSTRAGEM(veraseguir)


PRINCÍPIOBÁSICO:Divideapopulaçãoem"estratos"ealocaunidadesamostraisdentrodecadaestrato

DEFINIRESTRATOSInternamentemaishomogêneosqueentre

AMOSTRAGEMALEATÓRIAESTRATIFICADA

QUANTIFICAROSESTRATOSPRÉ:SeosfatoresdaestratificaçãojáforemconhecidosPÓS:Seosfatoresnãoforemconhecidosapriori

PROCEDIMENTOS:

AMOSTRAROSESTRATOSDentrodecadaestrato,aamostragemdeveseraleatória

Mas,precisamanterumnúmeromínimoderéplicasemcadaestrato(Gotelli&Ellison~=10)

Fazeraamostragemequitativaouproporcionalaosestratos?

Alocaçãoequitativaémaisútilquandosequerestimativasigualmenteprecisasparatodososestratosouparaapopulaçãogeral

AnaliticamentemaisfácildelidarcomnúmerosiguaisdeUAs

Fazeraamostragemequitativaouproporcionalaosestratos?

Alocaçãoproporcionalémaisútilquandoosmaioresestratossãoosmaisimportantes

SEFORPOSSÍVELSEGUIRTODOSOSPROCEDIMENTOSINDICADOS:

VANTAGENS:

-ÉPOSSÍVELUTILIZARAMÉDIAEAVARIÂNCIACOMOESTIMADORES

-MELHORAMUITOASUAESTIMATIVACOMUMNÚMEROMENORDEUNIDADESAMOSTRAIS


Other sampling designs take into account het-erogeneity in the population from which we aresampling. Stratified sampling is where the popu-lation is divided into levels or strata that repre-sent clearly defined groups of units within thepopulation and we sample independently (andrandomly) from each of those groups. Forexample, we may wish to estimate characteristicsof a population of stones in a stream (our variablemight be species richness of invertebrates). If thestones clearly fall into different habitat types, e.g.riffles, pools and backwaters, then we might takerandom samples of stones from each habitat(stratum) separately. Stratified sampling is likelyto be more representative in this case than asimple random sample because it ensures that themajor habitat types are included in the sample.Usually, the number of units sampled from eachstratum is proportional to the total number ofpossible units in each stratum or the total size ofeach stratum (e.g. area). Estimating populationmeans and variances from stratified samplingrequires modification of the formulae provided inChapter 2 for simple random sampling. If sam-pling within a stratum is random, the estimate ofstratum population mean is as before but the esti-mate of the overall population mean is:

ystr! Wh yh (7.1)

where there are h!1 to l strata, Wh is the propor-tion of total units in stratum h (often estimatedfrom the proportion of total area in stratum h)and yh is the sample mean for stratum h (Levy &Lemeshow 1991). If our sample size within eachstratum is proportional to the number of possibleunits within each stratum, Equation (7.1) sim-plifies to:

ystr! (7.2)

where there are i!1 to nh observations sampledwithin stratum h, yhi is the ith observation fromthe hth stratum and n is the total sample sizeacross all strata. The standard error of this meanis:

systr! (7.3)!"

l

h!1 (Wh)2

sh2

nh

"l

h!1 "

nh

i!1yhi

n

"l

h!1

where sh2 is the sample variance for stratum h.

Approximate confidence intervals can also bedetermined (Levy & Lemeshow 1991, Thompson1992). When statistical models are fitted to datafrom stratified sampling designs, the stratashould be included as a predictor variable in themodel. The observations from the different stratacannot be simply pooled and considered a singlerandom sample except maybe when we have evi-dence that the strata are not different in terms ofour response variable, e.g. from a preliminary testbetween strata.

Cluster sampling also uses heterogeneity inthe population to modify the basic random sam-pling design. Imagine we can identify primarysampling units (clusters) in a population, e.g. indi-vidual trees. For each primary unit (tree), we thenrecord all secondary units, e.g. branches on eachtree. Simple cluster sampling is where we recordall secondary units within each primary unit. Twostage cluster sampling is where we take a randomsample of secondary units within each primaryunit. Three stage cluster sampling is where wetake a random sample of tertiary units (e.g. leaves)within each secondary unit (e.g. branches) withineach primary unit (e.g. trees). Simple random sam-pling is usually applied at each stage, althoughproportional sampling can also be used. Thesedesigns are used to estimate variation at a seriesof hierarchical (or nested) levels, often represent-ing nested spatial scales and nested linear ANOVAmodels are often fitted to data from two or morestage cluster sampling designs (Section 9.1).

Systematic sampling is where we choose sam-pling units that are equally spaced, either spa-tially or temporally. For example, we might chooseplots along a transect at 5 m intervals or we mightchoose weekly sampling dates. Systematic sam-pling is sometimes used when we wish to describean environmental gradient and we want to knowwhere changes in the environment occur. Forexample, we want to measure the gradient inspecies richness away from a point source of pol-lution. Simple random sampling away from thesource might miss the crucial region where thespecies richness undergoes rapid change.Sampling at regular intervals is probably a betterbet. Various methods exist for estimating meansand variances from systematic sampling,


adiciona-seumtermodepeso(W)paracadaestratoh

-RESOLVEOPROBLEMADEAMBIENTESRAROS


SOLUÇÕES:

-ANALÍTICAS(PÓS-ESTRATIFICAÇÃOcomdadosadicionais)-MEDIÇÕESADICIONAIS-OPÇÃOPOROUTROSESQUEMASDEAMOSTRAGEM

-NOCASODEHETEROGENEIDADEPERCEPTÍVEL


Necessidadedeconhecimentoprévioe/oudetomadadedadosadicionais

-NOCASODEHETEROGENEIDADEIMPERCEPTÍVEL Errono"grão"paradefinirestratos

PRINCÍPIOBÁSICO:Apartirdeumpontoinicial,asunidadesamostraisestãoespalhadasaumadistânciafixa

AMOSTRAGEMSISTEMÁTICA

http://www.fao.org/forestry/11649/en/

PROCEDIMENTOS:

-DEFINIROESPAÇAMENTO

VANTAGENS:


-FÁCILEXECUÇÃO

-ACESSOFACILITADOAOSPONTOSDEMEDIÇÃO/FÁCILRECUPERAÇÃOPARARECENSOS

-ESPALHAMELHORASUNIDADESAMOSTRAIS(INTERSPERSÃO)-Maiorrepresentatividade

-PODESERASSOCIADACOMOUTROSESQUEMASDEAMOSTRAGEM

-ADEQUADAPARAREVELARMUDANÇASAOLONGODEGRADIENTES



-DEPENDÊNCIAENTREUNIDADESAMOSTRAIS,ADEPENDERDADISTÂNCIAENTREELAS

-SINCRONIAINDESEJADACOMALGUMFATORAMBIENTAL

-DIFICULDADEDEDEFINIROGRAUDEESPAÇAMENTO

ESCALA(GRÃOEEXTENSÃO)

GrãoPequenoXExtensãoPequenaGrãoPequenoXExtensãoGrande

GrãoGrandeXExtensãoGrande

GrãoGrandeXExtensãoPequena

SOLUÇÕES:

-MEDIÇÕESADICIONAISANTERIORES(Evitarsincronia;definirespaçamento)-ASSOCIARCOMOUTROSESQUEMASDEAMOSTRAGENS-ANALÍTICAS(PÓS-ESTRATIFICAÇÃO;SERPENTINA)


Existemformasanalíticasdeincorporaroefeitodaamostragemsistemática

Manly2008

Environmental Sampling 41

of as the local sampling errors. With a systematic sample of size n, there are n − 1 such squared differences, leading to a combined estimate of the vari-ance of local sampling errors of

s y y nL i i

i

n2 1

2 12

1

1�

�¤( ) ( )/ (2.28)

On this basis, the estimate of the standard error of the mean of the systematic sample is

SÊ(y) = sL/√n (2.29)

Site Boundary

FIGURE 2.4Grouping sample points from a systematic sample so that it can be analyzed as a stratified TBNQMF��5IF�TBNQMF�QPJOUT�r�BSF�HSPVQFE�IFSF�JOUP��TUSBUB �FBDI�DPOUBJOJOH�TJY�QPJOUT�

Site BoundaryStart of Line(point 1)

End of Line(point 60 )

FIGURE 2.5Defining a serpentine line connecting the points of a systematic sample so that the sampling variance can be estimated using squared differences between adjacent points on the line.

Environmental Sampling 41

of as the local sampling errors. With a systematic sample of size n, there are n − 1 such squared differences, leading to a combined estimate of the vari-ance of local sampling errors of

s y y nL i i

i

n2 1

2 12

1

1�

�¤( ) ( )/ (2.28)

On this basis, the estimate of the standard error of the mean of the systematic sample is

SÊ(y) = sL/√n (2.29)

Site Boundary

FIGURE 2.4Grouping sample points from a systematic sample so that it can be analyzed as a stratified TBNQMF��5IF�TBNQMF�QPJOUT�r�BSF�HSPVQFE�IFSF�JOUP��TUSBUB �FBDI�DPOUBJOJOH�TJY�QPJOUT�

Site BoundaryStart of Line(point 1)

End of Line(point 60 )

FIGURE 2.5Defining a serpentine line connecting the points of a systematic sample so that the sampling variance can be estimated using squared differences between adjacent points on the line.

usaessavariânciacorrigidaparaestimaroerropadrão

VÁRIOSOUTROSESQUEMASDEAMOSTRAGEM

AMOSTRAGEMANINHADA

AMOSTRAGEMMULTI-ESTÁGIOS

AMOSTRAGEMREPETIDA

ESTIMATIVADERAZÃO(RATIO-ESTIMATION)

AMOSTRAGEMADAPTATIVA

CAPTURA-RECAPTURA

AMOSTRAGEMROBUSTA->DETECTABILIDADE

TAMBÉMCOMBINAÇÕESENTREDIFERENTESESQUEMAS

PRINCIPAISREQUISITOSDEUMABOAAMOSTRAGEM:

-UNIDADESAMOSTRAISALOCADASDEFORMAALEATÓRIA-NÚMERODEUNIDADESAMOSTRAISDEVESER"SUFICIENTE"(LeidosGrandesNúmeros)-UNIDADESAMOSTRAISINDEPENDENTES

PODEMOSUTILIZARAAMOSTRAPARAESTIMAROSPARÂMETROSPOPULACIONAIS

Númeroadequadodeamostrasealeatorizaçãodevemsempreandarjuntos!!


Oeste(W)

Sul(S) Norte(N)

Vocêidentificapotenciaisproblemasnaamostragemanteriorquerealizou?

Gostariaderealocaras10unidadesamostrais?Indiquenafiguracom#Gostariaderealocaras60unidadesamostrais?Indiquenafiguracom+

Apósacoletadosdadosdanossaplanta,notamosqueexisteuma

variaçãomuitograndenaproduçãodesementes,mesmoconsiderandoas60unidadesamostraisestabelecidas.

Quaisfatorespoderiamestardeterminandoessavariação?


Oeste(W)

Sul(S) Norte(N)

Comovocêalocariaagoraas10unidadesamostrais?IndiquenafiguracomzComovocêalocariaagoraas60unidadesamostrais?Indiquenafiguracom*

SeráquepodehaverdiferençasentreasfacesNeS,emfunçãodaradiaçãoincidentesobreasfolhas,afetandoafotossínteseeareprodução?

Encontramosdiferençassignificativasnaproduçãodesementesentreunidadesamostraislocalizadasnafacenorteenafacesul

Qualoprocesso/mecanismoquedeterminaessasdiferenças?


Oeste(W)

Sul(S) Norte(N)

SeráqueasdiferençasentreasfacesNeSsãoemfunçãodoressecamentodosolo?


Oeste(W)

Sul(S) Norte(N)

Comosepararoefeitodaradiaçãosobreasfolhaseoefeitodoressecamentodosolo?

DELINEAMENTOSPARAESTUDOSEXPERIMENTAIS(nãoexclusivamente)

VARIÁVEISPREDITORASSÃOMANIPULADASEISOLADASDEOUTROSFATORES

DELINEAMENTOSEXPERIMENTAIS

OQUEMUDA?

DELINEAMENTOSEXPERIMENTAIS

OQUEMUDA?

PREMISSASMAISRÍGIDAS:

-Seleçãodasunidadesexperimentaiseatribuiçãodostratamentossãoindependentesdasvariáveisrespostadeinteresse

-Efeitosaleatórioseerrosexperimentaissãoindependentes

-Efeitosaleatórioseerrosexperimentaissãoigualmentedistribuídos,comoumavariávelaleatóriacommédiazero

TRÍADEDEPROCEDIMENTOSEXPERIMENTAIS

REPLICAÇÃO-ALEATORIZAÇÃO-CONTROLE

IDEALMENTENÃOEXISTEMFATORESDECONFUSÃOEMUMEXPERIMENTO(True-experiment)

ReplicaçãoeAleatorizaçãodevemsempreandarjuntas!!

DIFERENTESTIPOSDECONTROLE:CONTROLEDEEFEITO-SemaaplicaçãodotratamentoCONTROLEDEPROCEDIMENTO-Gaiolassemtelas-Garrafassemfuros-Shamsurgery

ALEATORIZAÇÃOSIMPLES-UMFATOR

PRINCÍPIOBÁSICO:Qualquerréplicatemamesmachancedeterumtratamentoatribuídoaela

-ANALITICAMENTEFÁCILLIDARCOMNÚMEROSDIFERENTESDERÉPLICASPORTRATAMENTO

ÉodelineamentobásicoparaaANOVAdeumfator

BLOCOSALEATORIZADOS

PRINCÍPIOBÁSICO:Alocatratamentosaleatoriamentedentrodeblocos

Minimizaachancedealgumefeitodesconhecidoatuaremapenasumtratamento

ÉodelineamentobásicoparaaANOVAaninhada(Nested)

Blocosnãorepresentamumoutrofatorconhecido

up six wood frame cages in the littoral zone andapplied one of six competition treatments (lowdensity Asynarchus, low density Limnephilus,high density Asynarchus, high density Limnephilus,high density both species, control with no caddis-flies) to each cage within each pond. The role ofhydroperiod (permanent or autumnal) was inves-tigated by having four ponds in each category. Theresponse variables were body mass and survival ofeach species analyzed separately, so there wereonly three density treatments (those containingthe same species). So there are two factors: hydro-period was “applied” (non-experimentally) towhole ponds (plots) and is termed the betweenplots factor and density treatment was applied tocages within plots and is termed the within plotsfactor. Split-plot designs are characterized byhaving factors applied to experimental units atdifferent, usually spatial, scales.

There are a number of practical design issuesfor this experiment.

• The experimental design that would be sim-plest to analyze would be to have whole pondsthat are subjected to levels of both factors,hydroperiod and density treatment, forming acompletely randomized (CR) factorial arrange-ment of two hydroperiods by six density treat-ments with n ponds per cell. Ponds are largeunits and we would expect considerable vari-ability between them, resulting in large resid-ual variance.

• It is often difficult to install cages, especiallylarge ones. For example, covering whole pondswith cages to maintain experimental densities

would be very expensive to set up and probablyrequire an immense amount of labour. Wemay find that we cannot physically deal withthe required size of cages in the time availableto set the experiment up, because the researchgrant has dried up, or we’ve exhausted thesupply of eager volunteers in earlier experi-ments. We would also need a lot more ponds.The current design uses eight ponds, whereas acompletely randomized design with even onlytwo ponds per density and hydroperiod combi-nation would need 24. That many ponds maysimply not exist.

• The split-plot design chosen allows us to groupour density treatments within ponds, minimiz-ing spatial variation in environmental charac-teristics, and giving us a clearer test of theeffects of density. It also reduces the size ofcages. We have, however, linked togethergroups of cages, and changed our statisticalmodel dramatically compared to the CRdesign. If anything happens to a pond (e.g. itdries up at the wrong time, or gets an algalbloom), we would be forced to discard all cagesin that pond. If we’d used a CR design, wewould lose just a single replicate in a cell.

As another example, Leonard et al. (1999) testedthe prediction that flow had strong effects on theabundances of mussels and barnacles in anestuary but that these effects might vary withtidal height. They had a number of general designoptions for testing this prediction.

• They could have sampled a range of sites in theestuary. In the simplest case, they could

302 SPLIT-PLOT AND REPEATED MEASURES DESIGNS

Figure 11.1. Diagrammaticrepresentation of the split-plotexperiment from Wissinger et al.(1996).There are four ponds (onlytwo shown here) in each of twohydroperiods (permanent andautumnal, represented by differentshading), the between plots factor.Within each pond, there were sixcages, each containing one level ofthe within plots factor, competitiontreatment.

SPLIT-PLOT

-PRINCÍPIOBÁSICO:Umaréplicadecadaníveldetratamentodeumdosfatoresdoexperimentoemcadaréplicadosegundofator.Casoparticulardeblocos.

Fator1:05antifúngicosdiferentesinjetadosempeixesemgaiolaseumcontrole(06níveis)

Fator2:02tiposdelagos(cinza=lagosprofundos;branco=lagosrasos)

Exemplo

MULTIFATORIAL-DOISFATORES(comváriosníveiscada)

-PRINCÍPIOBÁSICO:Ostratamentossãocompletamentecruzadoseortogonais.Todoníveldetratamentodoprimeirofatorérepresentadocomtodososníveisdosegundo

Onúmerodecombinaçõeséexponenciale,seconsideraronúmeroderéplicasnecessáriasparacadacombinação,podetornaroexperimentoinviável(economicamenteeemtermosdeesforço)

Atençãoàscombinaçõesquenãofazemsentido...

CuidadocomoESFORÇOAMOSTRALnossplit-plotenosmultifatoriaisAumentosmuitorápidos...

June 1984 PSEUDOREPLICATION AND EXPERIMENTAL DESIGN 193

Example 4. We return to our l-m isobath to testwhether oak. (Quercus) leaves will decompose morerapidly than will maple (Acer) leaves at that depth.This will be a manipulative experiment, though ouroperations in the field will be very similar to those ofour earlier mensurative experiments (Examples 2, 3).Now we are actually altering a single variable (species)and not just comparing a system property at two pointsin space or time.

We place eight bags of maple leaves at random with-in a 0. 5-m2 plot (A) on the 1 -m isobath and eight bagsof oak leaves at random within a second “identical”plot (B) contiguous to the first one. Because the treat-ments are segregated and not interspersed, this is anuninteresting experiment. The only hypothesis testedby it is that maple leaves at location A decay at adifferent rate than do oak leaves at location B. Thesupposed “identicalness” of the two plots almost cer-tainly does not exist, and the experiment is not con-trolled for the possibility that the seemingly small ini-tial dissimilarities between the two plots will have aninfluence on decomposition rate. Nor is it controlledfor the possibility of nondemonic intrusion, i.e., thepossibility that an uncontrolled extraneous influenceor chance event during the experiment could increasethe dissimilarity of the two plots.

Example 5. We use eight leaf bags for each speciesand distribute them all at random within the same ploton the 1 -m isobath. This experiment will allow us val-idly to test whether the two species decompose at thesame rate at this location. If our interest is primarilyin a comparison of the two species, we may feel thisexperiment is sufficient, and it is. However, if it isimportant to us to state how the two species’ ratescompare on t h e 1 -m isobath, then we should carry outan experiment in which both sets of leaves are dis-persed over two or more randomly selected points onthe l-m isobath. Also, if we wish to generalize to thel-m isobaths of a certain class of lakes, obviously twosets of leaf bags must be distributed in some random-ized fashion over all or a random sample of these lakes.The appropriate dispersion of replicates is as importantin manipulative as in mensurative experiments.

Modes of spatial interspersionand segregation

Fig. 1 illustrates schematically three acceptable waysand four (not five; B-4 is equivalent to A- 1, with respectto the interspersion criterion) unacceptable ways ofinterspersing treatments in a two-treatment experi-ment. The boxes or experimental units could be aquar-ia on a laboratory bench, a string of ponds, or a rowof plots, with either real (structural) or imaginaryboundaries, in a field or in the intertidal zone. Eachunit is assumed to have been treated (fish introduced,insecticide applied, starfish removed) independent ofthe other units in the same treatment.

A-1 Completely Randomized WIHIlWIlBBcl

A-2 Randomized Block LIB Wcl WEI 04

A-3 Systematic •nWIlWIl~cl

B-1 Simple Segregation l ~~~ElElclEl

B-2 Clumped Segregation WWUU Ixl~cl------mm - - - - - - -

B-3 lsolative Segregation !BBWW! klOUO!iI CHAMBER 1 Imm----mm, C H A M B E R 2 1

-w-m---m

T

B-4 Randomized, but withinter-dependent replicates

B-5 No replication

FIG. 1. Schematic representation of various acceptablemodes (A) of interspersing the replicates (boxes) of two treat-ments (shaded, unshaded) and various ways (B) in which theprinciple of interspersion can be violated.

A few comments are now offered concerning eachdesign illustrated in Fig. 1.

Completely randomized design (A- 1). -Simple ran-domization is the most basic and straightforward wayof assigning treatments to experimental units. How-ever, it is not frequently employed in ecological fieldexperiments, at least not when the experimental unitsare large (ponds, l-ha plots, etc.). In these cases thereusually are available only a few experimental units pertreatment, replication as great as four-fold being un-common. In that circumstance, a completely randomassignment process has a good chance of producingtreatments which are segregated rather than spatiallyinterspersed. For example, the chances of the randomnumbers table giving us simple segregation (B- 1 in Fig.1) are 3 % when there is four-fold replication and10% when there is three-fold replication. I stronglydisagree with the suggestion (Cox 1958:71; Cochranand Cox 1957:96) that the completely randomized de-sign may be most appropriate in “small experiments.”Clearly we cannot count on randomization always giv-ing us layouts as “good” as A-l (Fig. 1).

Few examples of strict randomization leading to in-adequate interspersion of treatments are found in theecological literature. Perhaps experimental ecologistsfall primarily into two groups: those who do not seethe need for any interspersion, and those who do rec-ognize its importance and take whatever measures arenecessary to achieve a good dose of it. In Fig. 2 areshown three actual experimental layouts in which thedegree of interspersion seems unsatisfactory. Fig. 2-1is the only example I have found of poor interspersionhaving resulted from clearly specified and formally cor-rect randomization procedures. And even in this case,the experimental layout is only that of one block in afour-block randomized complete block design. For theother two experiments (Fig. 2-11, III) the authors did

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